Strawmanning means presenting the opposing view in the least charitable light, often so uncharitably that it does not resemble the view that the other side actually holds. The term of steelmanning was invented as a counter to this; it means taking the opposing view and trying to present it in its strongest form. This has sometimes been criticized because often the alternative belief proposed by a steelman also isn’t what the other people actually believe. For example, there’s a steelman argument that states that the reason organic food is good is because monopolies are generally bad and Monsanto having a monopoly on food could lead to disastrous consequences. This might indeed be a belief held by some people who are pro-organic, but a huge percentage of people are just falling prey to the naturalistic fallacy. 

Nonetheless, while steelmanning may not be perfect for understanding people’s true reasons for believing propositions, it is very good for coming to more accurate beliefs yourself. If the reason you believe you don’t have to care about buying organic is because you believe that people only buy organic because of the naturalistic fallacy, you might be missing out on the fact that there’s a good reason for you to buy organic because you think monopolies on food are dangerous.

However, and this is where steelmanning back and forth comes in, what if buying organic doesn’t necessarily lead to breaking the monopoly? Maybe upon further investigation, Monsanto doesn’t have a monopoly? Or there are multiple organizations who have copyrighted different gene edits so there’s no true monopoly? 

The idea behind steelmanning solitaire is to not stop at steelmanning the opposing view. It’s to steelman the counter-counter-argument as well. As has been said by more eloquent people than myself, you can’t consider an argument and counter-argument and consider yourself a virtuous rationalist. There are very long chains of counter^x arguments, and you want to consider the steelman of each of them. Don’t pick any side in advance. Just commit to trying to find the true answer. 

This is all well and good in principle but can be challenging to keep it organized. This is where Workflowy comes in. Workflowy allows you to have counter-arguments nested under arguments, counter-counter-arguments nested under counter-arguments, and so forth. That way you can zoom in and out and focus on one particular line of reasoning, realize you’ve gone so deep you’ve lost the forest for the trees, zoom out, and realize what triggered the consideration in the first place. It also allows you to quickly look at the main arguments for and against. Here’s a worked example for a question.

That’s the broad-strokes explanation of the method. Below, I’ll list a few pointers that I follow, though please do experiment and tweak. This is by no means a final product. 

• Name your arguments. Instead of just saying “we should buy organic because Monsanto is forming a monopoly and monopolies can lead to abuses of power”, call it “monopoly argument” in bold at the front of the bullet point then write the full argument in normal font. Naming arguments condenses the argument and gives you more cognitive workspace to play around with and also allows you to see your arguments from a bird’s eye view. 
• Insult yourself sometimes. I usually (always) make fun of myself or my arguments while using this technique, just because it’s funny. Making your deep thinking more enjoyable makes you more likely to do it instead of putting it off forever, much like including a jelly bean in your vitamin regimen to incentivize you to take that giant gross pill you know you should take. 
• Mark arguments as resolved as they become resolved. If you dive deep into an argument and come to the conclusion that it’s not compelling, then mark it clearly as done. I write “rsv” at the beginning of the entry to remind me, but you can use anything that will remind you that you’re no longer concerned with that argument. Follow up with a little note at the beginning of the thread giving either a short explanation detailing why it’s ruled out, or, ideally, just the named argument that beat it. 
• Prioritize ruling out arguments. This is a good general approach to life and one we use in our research at Charity Entrepreneurship. Try to find out as soon as possible whether something isn’t going to work. Take a moment when you’re thinking of arguments to think of the angles that are most likely to destroy something quickly, then prioritize investigating those. That will allow you to get through more arguments faster, and thus, come to more correct conclusions over your lifetime. 
• Start with the trigger. Start with a section where you describe what triggered the thought. This can often help you get to the true question you’re trying to answer. A huge trick to coming to correct conclusions is asking the right questions in the first place. 
• Use in spreadsheet decision-making. If you’re using the spreadsheet decision-making system, then you can play steelman solitaire to help you fill in the cells comparing different options. 
• Use for decisions and problem-solving generally. This method can be used for claims about how the universe is, but it can also be applied to decision-making and problem-solving generally. Just start with a problem statement or decision you’re contemplating, make a list of possible solutions, then play steelman solitaire on those options. 

Conducting research is essential for identifying high-impact interventions and assessing the effectiveness of existing strategies. Unfortunately, the historical impact of research within the animal welfare space has been limited by poor quality studies, a lack of experienced researchers, and organizations’ lack of responsiveness to findings. In this report, we consider various approaches to animal welfare research and their prospects of being translated into positive impact for animals.

This report identifies nine crucial considerations regarding the funding and talent landscape of the animal welfare movement. These considerations are used to evaluate 16 potential paths to using research to enhance the impact of the movement. The report analyzes the interrelationships between the actions of researchers and NGOs and summarizes some historical evidence regarding the influence of research on the effectiveness of activist movements. 
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Of the approaches considered, we think that research that informs existing corporate campaigns is among the highest impact paths for research. For example: should activists prioritize demanding that corporations keep chickens cage-free, slaughter chickens less painfully, or nutritionally fortify their chicken feed? Research that helps corporate campaigners identify which of these asks makes a bigger difference to the welfare of the animals could double or triple the impact of the considerable resources invested in these campaigns. 

Another important finding was the importance of a research agenda that influences funding landscapes, which would potentially direct money from lower to higher impact interventions and shift the incentives under which organizations operate. This would involve surveying larger and more well-informed funders to determine what types of research would further improve their funding decisions and then conducting that research. This methodology could be used in parallel with many other research strategies. 
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Some additional paths that we considered include research coordination, randomized control trials on animal welfare interventions, deeper reports and summaries on interventions, and improving impact evaluations for existing animal organizations. These were assessed to have less potential for impact.
The full report includes a summary of our research, taking into account the uncertainties associated with different types of campaigns.

​​In my work as a research analyst for Charity Entrepreneurship, I have been assessing possible animal welfare campaigns. The first thing I found is that finding the correct welfare asks for corporate or government campaigns is really hard. The scarcity of information in animal advocacy relative to other cause areas means that accurate decisions are harder to make. Establishing reliable metrics to assess ideas is essential to avoid wasting time. One way of doing this is to think about how to approximate the endline metric we are trying to maximise: counterfactual impact. 

When trying to make the world a better place, what we really want to measure is the counterfactual impact. Counterfactual impact is the increase in utility that your actions actually cause in the world. If you are choosing to do X action, the actual impact that can be attributed to your action is the difference in utility between the world where you do X and the world where you do not. This is very difficult to measure, as your actions have flow-through effects, which have flow-through effects, and so on. Every action you take ripples out through the butterfly effect to change all of history. The way we account for this is by discounting these flow-through effects based on uncertainty until effects with an unknown direction are discounted to 0. Peter Hurford has written a more fleshed-out discussion of different ways to handle these flow-through effects.

Given that counterfactual impact is what we are pursuing, I have considered two possible strategies for selecting welfare asks: Maximizing the value of counterfactual speed-up and maximizing the welfare increase.

The simplest method could be considered as an instant-gratification method. For this method of decision making, we just choose the biggest welfare increase available to achieve as much welfare in the present as possible. If we use this method then, irrespective of what other organisations are doing, we should select the largest welfare increase available to us. If dissolved oxygen for fish is the largest welfare improvement possible, we should select it, even if we know that it is the next ask for which the rest of the animal movement will campaign. This may only speed the process up by a year, but it will minimise fish suffering in the present. 

Counterfactual speed-up is the second strategy. To select asks using this methodology, we need to know one additional piece of information: the time until other actors currently in the field would have chosen this ask. This timeline for welfare improvements allows us to calculate how much sooner our campaign caused the welfare improvement to occur.  

For example, imagine we are in 1975, considering a cage-free ask in the United States that would take 10 years to be successful. Knowing what we do now, we could see that conducting a corporate campaign at that time would speed up the timeline for cage-free by ~30 years. If we ignore the possibility of recidivism, by acting in the 1975s we only increase the number of cage-free years by 30. Using this model, the impact we have for chickens is 30 multiplied by the magnitude of the welfare increase caused by cage-free farming. Using this factor in our decision making, we now have some time sensitivity. 

If the largest welfare improvements are many years away, both decision-making strategies will dictate the same asks. However, we can quickly see where these two strategies will diverge. Imagine we are only examining two possible welfare asks: one that is a moderate improvement that will not otherwise happen for some time, and another that is large but will occur shortly anyway. If we choose the moderate improvement, it will occur many years sooner than it otherwise would have. If we campaign for the large improvement, it will only occur a few years sooner than it would have without our involvement. This is suboptimal from the counterfactual speed-up perspective, as a moderate ask advanced by many years will speed up welfare more, and thus we will be responsible for more impact. The benefit of this model is that it is relatively simple, as only the expected value of the welfare improvement needs to be determined.

A short examination of these two strategies would lead us to believe that counterfactual speed-up is always the superior model. The time-sensitivity of this way of making decisions should increase the counterfactual impact of your actions. However, it is still just a heuristic for counterfactual impact, not a direct measure. This is not just in terms of nebulous flow-through effects, but also the effect of speed-up on other interventions. If we achieve a welfare ask sooner, other charities can conduct a different campaign in place of this one; and where that second campaign would have been conducted, another; and so on. 

Thus, the two main effects of conducting a welfare ask now are:

1) The speed-up of the welfare ask selected
2) The speed-up of all subsequent welfare asks

Imagine what would happen in the timeline where we conduct the year cage-free campaign in 1975.  Cage-free improvements for chickens now occur 30 years earlier. Assuming organisations follow the same timeline as before, when they would have had to conduct cage-free campaigns they can now campaign for broiler chicken or fish welfare. In fact, through a single campaign in 1975, you speed up every welfare ask that will occur until the end of animal agriculture.

As long as your use of funding does not slow down the timeline for subsequent campaigns, the impact of your cage-free ask could be 30 years of cage-free chickens and 10 years of broiler and fish welfare improvements. Therefore, if you only measure the counterfactual speed-up for your actions on cage-free, you underestimate your actual impact. This consideration led me to create a very simple model for the charity sector to examine how the two strategies mentioned above compare when trying to maximize counterfactual impact. 

To explore this, I created a model of the charity sector where there is currently only one charity working on welfare improvements. There are ten years until animal agriculture ends, and ten possible asks. Once each welfare improvement has been achieved, it is never reversed and will last the remainder of the 10 years until animals are no longer farmed. The magnitude of possible welfare asks that charities can choose from are between 1000 to -100, and vary randomly within that range. This is not a perfect model of the magnitude of difference in actual welfare asks or its distribution. A more accurate model would probably have very few asks that have very cost-effective improvements, with many more closer to 0. I included the possibility of negative asks because our understanding of animal welfare may lead us to accidentally decrease the welfare of animals. 

Given this is the space charities are working in, I examined how deciding our ask based on counterfactual speed-up and welfare increase affects the counterfactual impact of our actions. In the real world, we do not have perfect information about the magnitude of welfare asks or the timelines of organizations currently in the field. It is possible that some ways of making decisions perform better in lower-information environments, but I thought examining the ideal situation could still provide some insight.  

In the first case, I examined a world in which a Random Altruist charity is already works on welfare asks. This charity chooses randomly from the set of welfare asks; this could be similar to (although probably worse than) choosing asks based on salience and emotional impact. In this case, I modeled a sample of 30 random welfare ask ranges and selections. I found that entering the space with the welfare increase method leads to more optimal outcomes ~17% of the time. The counterfactual speed-up approach leads to more optimal outcomes ~60% of the time. The two models were equally good ~23% of the time. Therefore, if we did not have perfect information and so could not just pick the optimal ask, maximizing counterfactual speed-up is a superior strategy. No surprise there. 

However, I then examined how varying the strategy of the existing charity would change the outcome. If the existing charity follows the simple welfare increase approach, the results change. Now following the simple welfare increase strategy is the optimal outcome 100% of the time! This would be the same if the actor in the space is trying maximize counterfactual speed-up, as the best way to do this when alone is to choose the biggest welfare asks.

This outcome seems to suggest that the optimal decision-making strategy in imperfect information environment changes based on the strategy of the other charities in the sector. It seems that the better other organizations are at differentiating between strong and weak welfare asks, the better the welfare increase strategy becomes. However, if asks are currently selected closer to random then counterfactual speed-up is a much better heuristic. 

I am unsure how accurate existing organizations would have to be at maximising welfare for the welfare increase strategy to win out. A more complex model may be able to capture this by altering the accuracy of welfare selection. It could also vary the amount and accuracy of the information for the three possible actors in the system.

Author: ​George Bridgwater, CE's Research Analyst

We at Charity Entrepreneurship recently ran our first formal two-month charity incubation program in London, which resulted in the foundation of around five counterfactual new charities.
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This post provides a brief overview of the application process that we used to select our 13 program participants and its outcomes. The main goal of the application process was to identify the candidates most likely to successfully found and execute one of our recommended charity ideas. We hope that this post will be useful for future applicants and other organizations in the effective altruism (EA) community.

Our application process had five stages. These were, in chronological order (the time we estimate each applicant spent per stage is in brackets), as follows:

1. Application form (including a CV and three long-form questions with a maximum of 1,000 characters each) (~1 hour)
2. First interview (~0.5 hours preparation + ~0.75 hours interview)
3. First test task (~5 hours)
4. Second interview (~0.5 hours preparation + ~1.5 hours interview)
5. Second test task (~3 to 5 hours)

We coded the responses from the application form and the two interviews numerically, to the extent that this was possible, to avoid subjective biases from affecting the selection of candidates.

​The following table shows the correlations between the scores of all application rounds and being accepted to join the program. We find that the scores from the two interviews were slightly more highly correlated with being accepted to the program than the test task scores (~0.59 vs. ~0.47). The scores of the two interviews were strongly correlated with each other at 0.62, and the scores of the two test tasks were moderately correlated at 0.33. However, the correlation between the interviews and the test tasks was fairly low (~0.2). One plausible explanation for this finding is that the two interviews and the two test tasks successfully selected for different dimensions of ability, as was intended. 

Most of the time, the decision is not obvious. For example, China accounts for ~48% of the total global production of farm animals but received only a small percentage of funding and attention compared to the USA, which that accounts for only 1.95% of total production.

(FAO, 2016)

Does it mean that China should be prioritized over other countries? Given the political and legal situation, such as strict governmental regulation of NGOs or lack of animal protection laws, progress in this country might be less tractable. Additionally, with almost all large problems, the absolute scale of the problem isn’t the most important factor to consider. That’s because almost always, the relative impact of work in a given country is not going to be capped because we reach the maximum scale of animals that can be affected, but because it is going to be slowed down or stopped by other factors much faster than they will by the total capacity of the problem. For example, if in China there is only $100,000 of total funding for animal activism, it doesn't really matter how big the animal production is from the scale perspective as long as it’s much larger than we are likely to help effectively with $100,000.  
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Another example would be India. The country is responsible for almost 10% of the global animal production due to its extremely large population, and despite a high vegetarianism rate. It would be naive, however, to infer that India is highly promising for animal advocates purely based on this national production figure. Many policies to improve the lives of animals in India would be realistically implemented not on a national level but on the level of individual states; the same is true, of course, for large countries like the United States. Changing policies at the level of the Indian national government is immensely difficult and likely too intractable. In practice, animal advocacy groups operating in India should therefore mostly focus on changing state legislation, which is much more tractable. For this reason, figures on national-level animal production and human population might be misleading in cases like India and the US, and state-level figures are much more meaningful. Importantly, not all Indian states are created equal: After all, they vary in size from a large country (200 million in Uttar Pradesh) to a medium-sized city (1.5 million in Goa). These considerations matter a lot when we are comparing India to other countries. Nobody would think to compare Germany to Africa when choosing a country to operate in, yet India has a bigger human population than the whole African continent. When considering what location to work in, often there is more detail required than national population or animal production numbers. This is one of many examples illustrating why we tried to look at many factors simultaneously when selecting a country to work in.

Another issue when choosing the country is the difference between the net production of animal products and net consumption. When we analyze the data, the results show a correlation of only 0.35 between production and consumption of fish in a given country. That means only 12% of consumption in the given country is explained by the production. And indeed, the list of priority countries is different for those two variables. This means that a country should be prioritized based on the approach that is going to be used there. For example, Bangladesh is the fourth most promising country (from the scale perspective) to work in when addressing high production. Therefore, higher welfare standards for animals can be ensured through corporate outreach and governmental lobbying. However, Bangladesh is in the 116th place when analyzed from the perspective of the overall consumption of animal products, so focusing on individual change to promoting veganism or reducetarianism or increasing access to contraceptives is much less promising. 

Considering those factors and other factors, we came to the conclusion that the most promising countries to research deeper are those characterized by:
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1. A high number of priority animals produced or a high number of priority animals consumed 
2. High neglectedness — Calculated as a ratio of current funding (or theoretical $10,000) spent on animal advocacy to the number of animals produced/consumed
3. High tractability 
4. Low-scale limiting factors 
5. In the case of consumption: population size

For example, according to FAO’s data, Bangladesh seems to be one of the most promising countries. It accounts for 3.10% of the global production of animals, much more than the USA or any European country, where most of the animal advocacy organizations now operate. Additionally, Bangladesh seems to be progressive in its food policy. For example, Bangladesh was the first country to be approved for the commercial release of GMO crops. Approval was passed from the ministries of Environment and Forests (MoEF) and Agriculture (MoA). This suggests that those ministries might be progressive also on issues related to other aspects of agriculture.

Based on research into the above criteria, we’ve chosen 22 countries for a deeper dive to determine where we should start a charity. We researched each country individually and gave them a score on nine criteria:

1. Governmental regulation of NGOs Governmental regulation of NGOs 
2. Attitudes towards farmed animals
3. Type of farm animal production
4. Number of companies/ farms controlling the market
5. Presence of animal advocacy organization(s)
6. Animal protection laws and enforcement
7. Attitudes toward eating animal products
8. Other political and cultural challenges
9. English proficiency 

Based on this system, we think that:

• The top priority countries to focus on when funding a new animal advocacy charity regardless of the ask or approach are:

1. Canada
2. The USA
3. Taiwan
   
   

• Top priority countries to focus on when addressing problems with production are:

1. Brazil
2. Mexico
3. Japan
   
   

• Top priority countries to focus on when addressing problems with consumption are:

1. Australia
2. Lithuania

Although this list offers us a good overview of how promising a given country is, it is not the ultimate information you should base your decision on. It should be modified if you are planning to use a specific approach or an ask. For example, India might score above average if you take into account all the factors, but the regulation of NGOs seems particularly limiting. If you are planning to improve management of dissolved oxygen levels through governmental regulation, then India will be a particularly bad country because of relatively small fish production and the hostile stand on non-profit organizations. Comparatively, Taiwan might only be 0.2 SD better than India, but when we take into account their position on international NGOs, and more conducive regulations when it comes to policy-making combined with high fish production, it makes Taiwan much more promising. This research should be used as a starting point, not as an ultimate answer. 
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Our full spreadsheet, with all the ratings, as well as links to the 1-5-page summary reports, gives specific descriptions as to why certain countries received certain ratings. Each full report is a summary page with key information and is followed by a section of rough notes (generally in the 10-20 page range). Each report was time capped at five hours, so they are limited in both scope and depth. Therefore, we are keen to get more information on any of these areas that could change the prioritization.  

For some approaches, such as corporate governmental outreach, the impact of asks that might be implemented could be increased by expanding those new policies to a cooperating country, so we also grouped them based on the trading agreement between countries to provide additional input that will inform our decision and took an average score for the group. 

Many of these countries have a relatively limited animal charity presence and a small chance of developing it, which gives us more confidence there is room for additional counterfactual impact-focused charities to be founded. When considering the most important charities to found, we expect many, although not all of them, will be best founded in priority countries. We also expect some of these countries to change over time. For example, if a large charity was founded in Vietnam, that would change how promising the country is for new charities to be founded in the country and thus lower its priority.

Many thanks for Vicky Cox who contributed greatly to this research as a part of her internship at Charity Entrepreneurship by researching all the information needed to rate the countries on all criteria.

​In recent years, there has been an observable shift in the animal advocacy movement towards institutional change. Among other institutional strategies, corporate outreach seems widely used to achieve positive change for animals. Corporate outreach involves designated campaigns aiming to influence the behaviour of corporations.

This report focuses on estimating the impact of corporate outreach with the aim to assess the potential impact of a new charity which may be started to execute corporate outreach. Because of the very broad definition of corporate outreach, this report considers 13 sub-approaches in total. These include facilitating international expansion of existing animal organizations, e.g. The Humane League to Asia and Latin America; ensuring the following-through of existing corporate campaign pledges; and starting a new organization in a priority country advocating for a different issue than the existing confinement-based asks; etc.

We expect that corporate outreach is one of the most cost-effective interventions for animals, if paired with a high impact ask and executed correctly in a promising country. In line with our priority animal, priority ask, and priority country research, we expect the most promising charity that could be founded in this space is one focused on corporate campaigns for fish water quality in a country with a high fish population but with a relatively small corporate campaign presence, such as Taiwan.

Decision-making on which charities to establish involves certain complex processes. Part of this analysis is looking at the effectiveness of different  approaches. Currently at Charity Entrepreneurship, I am analysing how promising the corporate outreach campaigns are in implementing the most promising asks. Coming from a cluster approach perspective, I analyse multiple groups of evidence, one of which is historical case studies. This post explains an analysis about the counterfactual impact of cage-free corporate campaigns in the US. We use this case as one of thirty-five pieces of evidence we took into account in evaluating how promising the launch of new corporate outreach campaigns would be. This particular piece has limited weight in the decision-making process, so please do not interpret this in separation from the other evidence we are going to present in the following posts, which are:

1. Probability of follow-through once companies pledge a change in policy.
2. Cost-effectiveness of launching new corporate campaigns, specifically improving management of dissolved oxygen level in Vietnam.
3. Full report on corporate outreach including, but not limited to, evidence, execution difficulty, and cost-effectiveness.​

​In this piece of research, Charity Entrepreneurship identified and modelled crucial factors that could have contributed to the current percentage of cage-free eggs: historical trend, changes in the price gap between cage-free and caged eggs, the effects of consumer willingness to pay for higher welfare, and the price elasticity of demand. In another scenario, the effect of avian flu was also accounted for. We concluded that in 2017-2018, the above factors explained only ~6% of cage-free eggs produced, which leaves 10.4% of cage-free eggs that can be explained by corporate outreach (or other known and unknown factors, e.g. animal advocacy for reducing the consumption of cage eggs). In 2015, when the avian flu outbreak occurred, analysis left only 0.6% of cage-free eggs unexplained, which might suggest that there might have been a significant factor in the increase in cage-free eggs. Below, I elaborate on all factors researched and analyzed by me and CE’s research intern Vicky Cox, who played a crucial role in this research.

The first perspective we took into account is whether the observed 13% change in the percentage of cage-free in the US between 2005 and 2018 matched the percentage of eggs that were reportedly affected by the companies that pledged to switch to cage-free eggs.
Using information from the corporate commitment tracker (unpublished) and EggTrack’s report, we should see ~9% (8.67%) difference in the fraction of cage-free eggs between 2005 and 2018. So we could say that, at best, 9% of the egg market share could be explained by commitments made by companies. There are two problems with those number, however:

1. We found two companies in the progress towards cage-free (Campbell’s and Hormel), but no available data on the number of hens, and therefore the number of eggs, that this would affect. Consequently, this data cannot be added to the observed percentage.
2. There are a lot of companies on the corporate commitment tracker spreadsheet that are not on EggTrack, meaning that their rate of progress is unknown and therefore can’t be added to the observed percentage.

The above observations mean that the actual number of affected eggs might be higher.
For some of the companies on EggTrack, progress was given in a breakdown of shell egg progress and liquid/ingredient progress. We decided to weight these based on available information. Weighting of shell to liquid eggs in observed percentages:

• Compass Group: Compass uses 300 million liquid eggs and 100 million shell eggs each year (source). So the weighting was worked out as: 0.75(15)+0.25(88) = 33.25
  Where 0.75 comes from the fact that three quarters (300 million liquid eggs/400 total eggs) of Compass Group's production are liquid eggs.
  The 15 in brackets indicates the percentual  progress the company has done towards cage-free eggs in their use of liquid eggs (source).
• Sodexo: Sodexo uses 220 million liquid eggs and 39 million shell eggs each year (source). So the weighting was worked out as:
  0.85(16)+0.15(86) = 26.54
• Aramark: Aramark uses 200 million liquid eggs and 30 million shell eggs each year (source). So the weighting was worked out as:
  0.13(100) = 13
• Other companies that break their commitments down by shell and liquid eggs are:
  Starbucks
  Panera Bread
  Centerplate
  Ruby Tuesday

However, we do not have statistics for how many shell and liquid eggs each company uses each year. So, ultimately, we don’t have an obvious weighting. Since Centerplate is a foodservice like Compass Group, Sodexo and Aramark, we assumed that their usage of shell and liquid eggs is similar. Therefore, we used the following weighting (taking the average of the above 3 food services): 0.18(100) = 18
Starbucks, Panera Bread and Ruby Tuesday are all restaurants. We assume that they will use more shell eggs than liquid eggs. We arbitrarily weight this as: two-thirds shell, one-third liquid.
As a result, we concluded that at least 9% and maximally 13% of cage-free eggs could have been influenced by the corporations’ behaviour.

Another consideration we took into account is the fact that increases in the relative share of cage-free eggs might just be a matter of a historical trend and that the same increase would have be seen in the absence of corporate outreach campaigns. To estimate what would have been the proportion of cage-free eggs in 2016/17/18, we extrapolated from the historical trend.

In our analysis, we used extrapolation from data up to 2013, because that was the year that the first cage-free campaign started. Between the expected percentage of cage-free eggs that could be attributed to historical trend and the actual percentage of cage-free eggs, there is a 5.7% difference in 2016, 9.3% difference in 2017, and 10.1% difference in 2018. This is an 8.4% difference on average that cannot be explained by historical trends.

As pointed out by Šimčikas, in the year 2005 avian flu could have potentially pushed consumers into buying cage-free eggs instead of cage eggs by causing the price gap between generic eggs and speciality, cage-free eggs to close down quite dramatically. According to the report from the Economic Research Service, between December 2014 and June 2015, more than 50 million chickens (and turkeys) in the United States died of highly pathogenic avian influenza (HPAI) or were destroyed to stop the spread of the disease. These birds accounted for ~12% of the U.S. layer population - this could explain the initial spike in the percentage of cage-free eggs relative to caged-eggs that was observed in 2015. It is also possible that the decrease in cage-eggs created an illusion of increase in cage-free egg consumption. Layers accounted for a large majority of the lost birds. Over the May-December period in 2015, the benchmark egg price was 61 percent above that from a year earlier, while production declined only about 10 percent. Production was low despite at least 21 million layers being added to the national flock between June 1, 2015, and January 1, 2016, reflecting the relatively low layer productivity that delayed the recovery. However, by March 1, 2016, the flock expanded by another 9 million birds and lay rates improved, resulting in more or less normalised  levels of production. After the outbreak, record-high egg prices were the most notable market change, and price increases far surpassed production losses on a relative basis. Here, “normal levels of production” pertains to the production of cage-eggs. This is a point for the greater impact of the corporate campaigns, because a higher observable percentage of cage-free eggs in the following years is not a result of a decrease in cage eggs.

The expanded role of cage-free products may have also altered the supply and demand for eggs, and resulted in additional price volatility. While data on cage-free layers in 2016 was limited, between September 2015 and September 2016 over half of the estimated net increase in the national flock was due to more cage-free layers. Eggs are among the most price inelastic foods - their price elasticity is estimated to be 0.27 where a 95% confidence interval is given by (0.08, 0.45) (source). Assuming that this price elasticity holds, an increase of 61% in the price of eggs would have seen a 16.2% (4.88, 27.45) reduction in the quantity of caged-eggs consumed. If we assume that all of this reduction is made up of purchasing cage-free eggs instead, then cage-free eggs would see a 16.2% increase in demand.

To simulate consumer behaviour and influence over the percentage of cage-free eggs produced, we used studies on consumer willingness to pay for cage-free eggs. In a study on the market potential for cage free eggs by the Food Marketing Institute, Animal Agriculture Alliance, and the Foundation for Food and Agricultural Research, it was found that when provided no additional information, half of consumers are willing to pay no more than a $0.30/dozen premium for cage free eggs. The mean premium is $1.16/dozen, suggesting a small fraction of consumers are willing to pay sizeable amounts for the cage free label. Almost 60% of consumers have a willingness to pay for cage free less than $0.40/dozen, but 33% have a value greater than $1.00/dozen.
The results suggest there is potential for the market-share for cage free eggs to rise above the current state even at premiums as high as $1.00/dozen. However, even at much more modest price premiums, the potential for cage free eggs to attain the majority market share is unlikely, particularly if conventional egg sellers advertise other desirable attributes. When ranking the importance of factors that influence the purchase of eggs, price came first with 43% relative importance, while animal welfare came fifth behind safety, taste, and nutrition, with 8% relative importance.

The above study seems to be the most reputable as it has the most respondents (>2,000) and it is used as the main source for nearly all other articles and reports on consumer willingness to pay. Some other reports have roughly the same numbers, but possess much less respondents. For example, this report with 327 respondents saw results that 27% of respondents would be willing to pay a premium of $0.98 for cage-free. The respondents for this survey were college students, who would perhaps be more willing than the older generation to pay more for animal welfare, as younger people tend to care more about animal welfare. On the other hand, they might have a less stable financial situation and be averse to spending more.

Based on these studies, we concluded that ~30% of consumers were willing to pay premium on cage-free eggs in 2007 and 32% were willing to do so in 2018. We concluded that this 2% increase in cage-free eggs’ consumption resulted from consumers’ choices that would, overall, be partially independent from corporate campaigning.

It was observed that between 2014 and 2015, the per capita egg consumption dropped by ~4% (4.04) (source). That brought up another inquiry of interest: how might the complete removal of conventional eggs affect egg buying behavior? To explore this issue, it is now assumed that consumers have a choice between a conventional egg option (priced at $0.99/dozen), cage free eggs (priced at $1.79/dozen), and they also have the option to choose “none” and refrain from buying eggs altogether. As shown in the left panel of figure 9, under these assumptions, 59% are projected to choose conventional, 36% cage free, and 4% “none.” The right-hand panel of figure 9 shows the projections of what would happen were the lower-priced conventional option removed from the market. If this were to occur, the models predict the share of consumers who would refrain from buying eggs would increase from 4% to 17% (source, page 28). In case of such an increase in prices, 4% of consumers might refrain from purchasing eggs.

Price of caged eggs before and after the avian flu

​Preliminary research pointed out some inconsistencies, so we analysed multiple sources to estimate the increase in prices. The Report from the Economic Research Service shows a 61% increase in prices. When we look at the estimates, the 61% increase stated in the report is for consumer-grade eggs (fresh eggs on store shelves), but not for processing-grade eggs that are used by restaurants and others. Attempting to read prices off Figure 1, we see that the price of eggs in May 2014 is US$1.05 and the price of eggs in May 2015 is US$1.7. Taking these prices as accurate, this is ~61% (61.9) increase. Making the price of eggs in May 2015 1.69 instead of 1.7 makes the price increase 60.95%, even closer to 61%.

Looking at the benchmark price on all available USDA reports from May - December 2014 and taking an average, and looking at the benchmark price on all available USDA reports from May - December 2015, we have a 63.6% price increase.

The USDA, in a monthly supply and demand report, increased its forecast for the price of Grade A large eggs in New York in 2015 to $1.60 to $1.66 per dozen. That is up from its May estimate of $1.30 to $1.36, and tops last year’s average price of about $1.42, which was a record high, according to USDA data. In the fourth quarter of 2015, eggs will average $1.73 to $1.87 per dozen, up from about $1.63 a year earlier, the USDA said. Last month, the agency predicted a dozen eggs would cost $1.33 to $1.45 in the fourth quarter.

Summarising these three, we have:

1. Price spike in June 2015: $2.40 compared to $1.20 in June 2014. In May 2014, the egg price is $1.05 and increases to $1.69-$1.70 in May 2015.
2. Considering the benchmark prices from the USDA reports, prices increase from an average of $1.43 to an average of $2.34.
3. Taking the average price of eggs in 2014 from USDA’s report as $1.42, a 61% increase would mean that the average price of eggs in 2015 is $2.29.

Summarising:

• Price before: $1.28 (1.1, 1.46)
• Price after: $2.08 (1.77, 2.39)

Which gives us the 95% CI of price increase as: 62.5% (60.9, 63.7)


Absolute price of cage-free eggs during the 2014-15 period

We didn’t manage to find prices of eggs in 2014 and 2015, therefore used two separate methods, both of them have some limitations, so we think this part is especially prone to error. However, It doesn’t affect the main conclusions.

In 2015, it was found that, on average, cage-free eggs were 2.3 times more expensive than caged eggs (source).

Using these values to give us a CI we get:
2014 price: $2.94 (2.53, 3.36)
2015 price: $4.78 (4.07, 5.50)

Wholesale - the term seems to be synonymous with free-range - egg prices were in the $1.25 per dozen range in the fall of 2014, but by August of 2015 they had risen to $2.60 per dozen (source). The wholesale price of a dozen eggs fluctuated between $1 and $1.77 across the US in 2014, according to government statistics. Using Guesstimate, the average of this range is $1.40. The wholesale price of a dozen eggs in 2014 was $1.40 (source). Using the graph in this report, the price of wholesale eggs was ~$1.40 in 2014 and ~$1.80 in 2015.

Using these values to give us a CI we get:
2014 price: $1.36 (1.29, 1.43)
2015 price: $2.20 (1.42, 2.98)

Price of caged and cage-free eggs when avian flu stopped affecting prices

​It seems that avian flu stopped affecting the price of eggs in 2016. The largest gap in the prices of caged and cage-free eggs was in 2017. However, evidence suggests that the price gap closed in 2018. Since it seems that avian flu stopped affecting the prices in 2016, and there are no obvious outside factors that could explain the price gap closing in 2018, we assume that this might be the result of corporate campaigns.

In 2016, due to an oversupply, the average selling price for cage eggs was down 64.9% (compared to 2015 where prices increased due to avian flu). Although cage-free egg prices also fell, they were only down by 13.2% (compared to 2015 prices) (source). A fall in cage egg prices of 49.8% can be seen on Statista where the price of a dozen eggs was $2.75 in 2015 and $1.38 in 2016. As of May 6, 2016, the USDA National Retail Report reported that the advertised prices for shell eggs was $1.07 a dozen for white large USDA Grade A eggs while “cage-free” large white eggs sold at $2.49. This is a premium of $1.42.

A dozen conventional eggs in March 2017 cost an average of $1.05. This was reported to be ‘less than half’ as expensive as a dozen cage-free eggs, according to price data from the USDA (reported by CNBC, they weren’t more specific). Using data from Bloomberg below, we can estimate that whilst a dozen caged eggs cost $1.05, a dozen cage-free eggs were at $2.85 (this is a premium of $1.80).

According to USDA-Agricultural Marketing Service data, while the premium in 2018 is lower than it was in 2017, it is still a $1.28 premium. This suggests that perhaps the gap in prices is closing again (“while the premium is lower than last year”). This idea is also backed up in an article from Bloomberg which states that the price differential between cage eggs and cage free eggs is decreasing. Reasons for this gap closing seem as simple as many corporations having made progress on their cage-free commitments, which results in the increase in supply that reduces cage-free eggs’ premium over regular eggs.

Since the biggest price gap was seen in 2017, we will model prices off this year and compare them to the prices in 2018 when the price gap began to close. Using the same study as previously on the market potential for cage free eggs by the Food Marketing Institute, Animal Agriculture Alliance, and the Foundation for Food and Agricultural Research, it was found that ~30% of consumers would be willing to pay the premium of $1.80 (based off the graph on page 24/50). When the price gap started decreasing in 2018, the premium fell to $1.28, and at this price ~32% of consumers were willing to pay the premium. Since it seems as if avian flu had stopped affecting prices by 2017-2018, it seems as if this 2% increase in the number of consumers willing to pay for cage-free eggs is a result of corporate campaigns increasing the supply of cage-free eggs (making the premium smaller).

Based on the research above, we modelled all factors in Guesstimate, concluding that these factors explain only 6% out of 16% of all cage-free eggs, which leaves 10.4% to be explained by other factors, i.a. impact of corporate campaigns. However, we didn’t take into account other factors that might explain the increase, e.g. individual outreach or, more importantly, political change, particularly California’s Proposition 2 that passed in 2008 as a result of HSUS’s work. The Proposition, among other things, prohibits the confinement of hens in a manner that does not allow them to turn around freely, lie down, stand up, or fully extend their limbs, therefore effectively banning the usage of battery cages. Proposition 2 is credited as preparing the ground for the campaigns that followed with dozens of cage-free commitments from most companies in the US. Animal Charity Evaluators claims that Proposition 2 was the main factor that contributed to the success of the campaign against McDonald’s, which pledged policy change in 2015, preceding a series of cage-free commitments from other companies. Given that, ~10% is the upper confidence interval for the counterfactual impact of all of the campaigns in the US. To narrow down the confidence interval we used research by Founders Pledge on i.e. corporate outreach campaigns. They estimated that every cage-free campaign in the US that THL runs speeds up the commitment by 1-1.5 years on average. Using the data from Egg Track we estimated that the average percentage of eggs affected in 2017-18 is ~0.015%. Therefore, the total percentage of eggs affected by THL by speeding up every cage-free campaign is ~0.015% to ~0.023%. According to ChickenWatch, there were 76 commitments taken in 2017 and 35 in 2018, giving us 111 in total. Therefore, the total effect of THL between 2017-18 is ~1.71% to ~2.56%, which we are going to use as a lower band of the confidence interval, giving us ~2.1- ~10% of the counterfactual impact of corporate campaigns.

Different results can be observed from our similar analysis of the period affected by the avian flu. Here, the percentage of cage-free eggs unexplained by all the factors taken into account in the previous analysis and the impact of the avian flu is only 0.6%. That might provide the argument for the hypothesis that the disease outbreak made the transition easier by closing the price gap between eggs from different housing systems and forcing some producers to partly switch to cage-free systems, which offered greater food safety. Given how surprising the result was for us, we conducted sensitivity analysis and double-checked the factors that were the sources of the greatest uncertainty in the final outcome. We listed potential flaws with those estimates:

• Price elasticity of eggs: the number is taken from a literature review which estimated this number from a sample size of 13 (some other food products have a sample size of ~50). Therefore, the expected percentage decrease in cage-eggs might be wrong;
• Extrapolation of the historical trend could be wrong;
• Rounding errors: for example, observed change is 8.67 but rounded to 9;
• Price of cage-eggs before and after avian flu was difficult to estimate: an average of USDA benchmark prices over the May-December period of 2014 and 2015 was used as one of the three sources to find these prices, the number of reports in this time period varied (there were 9 reports in 2014 and 5 reports in 2015, so there was a larger sample size in 2014);
• Percentage of people who won’t purchase eggs after the price increase of cage-eggs could be too small; maybe more would switch to cage-free instead.​

The presence of all analyzed factors, if no other factors play a role, would result in 6% of all eggs in the US being cage-free. However, we can observe that ~16% of eggs produced in the US are cage-free eggs, which means that the effects of other factors result in an additional 10.4% of cage-free eggs. This could be explained by corporate outreach (or other known and unknown factors, e.g. change in legislation that increased the probability of the success of the campaigns). Therefore, we attribute the counterfactual impact of corporate campaigns to be between 2.1-10% of eggs being switched to cage-free. We are not going to use this number in the cost-effectiveness analysis separately from other factors. We plan on publishing an analysis of expected success of launching new corporate campaign, and this piece is only a supplementary element to the bigger research on corporate outreach.

Although we will not do this ourselves, we would love to see a similar analysis for a different country, and we suggest the UK given the availability of data. If anyone is interested in doing so, we would love to send you any data we might have to help get you started. We gathered data on the relative share and number of cage free-cage eggs in the UK and it can be found here.

If most corporations tend to follow through with their corporate social responsibility pledges, starting a new charity that campaigns for welfare improvements for animals would be one of the highest impact opportunities out there. But what if only a tiny fraction do? Then, it might not be worth investing in. This is why one of the key crucial considerations, when considering the launch of a new corporate outreach campaign, is the ability to enforce the pledges and ensure that companies follow through on their commitments to improve animal welfare. There are some concerns that commitments have been broken, or will be, and therefore the impact of past campaigns is significantly reduced.

To estimate the expected value of launching a new corporate campaign, we need to first estimate the probability of companies following through with their commitments. We approached answering this question using a cluster approach, looking at the issue using many different sources of evidence: historical evidence, industry expert opinions, animal advocacy and effective altruism expert opinions, and studies. Below, we offer a summary of conclusions from this research. The color coding represents the type of update each group of evidence gave us. Green denotes a generally positive update (making us more confident in the odds of corporate follow through), yellow stands for a neutral update, orange for a minor negative update, and red for a more negative update. Gray is where information was unavailable. Taking into account all the evidence, we estimated that on average ~44% of companies will follow through on their welfare commitments.

​A 39% - 50% confidence interval is going to be used to model cost-effectiveness of launching another corporate campaign. It is not an estimate about effectiveness of past corporate campaigns on egg-laying hens and broilers issues!
The full model can we seen here. You can copy it and insert your inputs on the weight of evidence and strength of direction of a given parameter.

These charity summaries are very short summaries, normally based on several reports on the most important sub-elements: the specific animal, ask, approach, and country report. Some of these reports are not published yet, but when they are, they will be linked in this summary. Reports that have been or will be researched but are not yet published are marked with a * to show where future reports will be linked. The summaries are created to give an idea of the recommended charity, but they are not aimed at giving a full justification. Those longer reports will be published later and are thus marked with a *. The order of these charities does not reflect the promisingness of the specific charity. The color coding represents areas of higher or lower certainty. Green represents the areas we are fairly confident will not change, and red represents currently tentative conclusions that could change in the next month. Please note, these charity recommendations are our best guess based on research we have conducted so far (conducted over the span of a single year). That being said, the proposed interventions might change within the next two months as a result of further research we will be conducting. The degree of uncertainty is represented by the color coding. Nonetheless, even the most certain ideas will be revised and could potentially be removed or substantially changed.

Click to see a version with full links

• Institutional ask research*

​
One of the biggest historical successes in the animal space has been the impact of institutional change. Both corporate and governmental campaigns seem to have the ability to affect huge numbers of animals with significant welfare improvements. One of the important parts of these campaigns is making sure the change being asked of a governmental or corporate body is a change that is significantly beneficial for animals. Some asks can be significantly more impactful than others, and careful consideration and research should be put into comparing all the possible asks. A dedicated organization that is focused on researching possible institutional asks could more than double the impact of a large scale campaign through a relatively small investment of funding and time. Making these decisions can benefit from current research. However, no organization is specifically focused on this research topic full-time. For example, there has been relatively little public, numerical comparison of an intervention like dissolved oxygen for farmed fish and how its welfare benefits would compare to a change in slaughter methods. Our initial models suggest that there could be an extremely large difference in animal welfare depending on which of these interventions is selected for a campaign. Given that campaigns* such as this one would generally take years and millions of dollars, 6 months of full-time research with a small team is a very worthwhile investment for the animal movement to make before launching such a campaign. Similar situations occur often enough, like the recent cage free and broiler chicken asks, to suggest that there could be ongoing high impact research that could be done in this area.​

• Fish water quality corporate campaigns*

After recent progress with corporate campaigns focused on both egg laying and broiler chickens, the clearest next targets for a corporate campaign by our estimates are farmed fish and wild fish caught for human consumption. Fish are both extremely numerous and have a very low welfare score, and historically, comparatively little attention has been paid to fish by the animal movement. More specifically, water quality at non-optimal dissolved oxygen levels is one of the main causes of suffering that occurs among farmed fish. This issue is particularly important with the growing popularity of farmed fishing relative to wild fish consumption and given the relative ease and low cost of implementing such a change. An organization focused on fish water quality could help coordinate such a campaign in partnership with larger organizations. An organization solely focused on this issue could also work more directly in locations outside of the EU and USA if they are focused on a country with a high fish population but with a relatively small corporate campaign presence, for example, Vietnam. This would be a new model and could provide more expertise for every future presence-oriented corporate campaign working in a particular country, as well as test a possible structure for expanding corporate campaigns into countries outside of the ones they have worked in so far.

• Feed fortification of egg-laying hens*
  
  

The main causes of mortality for egg-laying hens are bone fractures, disease, malnutrition, osteoporosis, and pecking; all appear painful and involve long periods of suffering. These problems occur on farms with battery cages, enriched cages, and even in the cage-free system*. Given how prevalent it is in all systems of hen farming, a direct solution to this problem is needed. Feed fortification is an unusually direct and cost-effective way of addressing this major source of suffering - particularly bone fractures and osteoporosis. The most promising nutrients for chickens, that are also cost-effective to use, are phosphorus, calcium, and vitamin D3. Given that the high cost of feed accounts for 60 to 75% of the total production cost, farmers should be able to easily include a cheap premix in their feed or accept the whole feed (with additional vitamins). Approaching farmers directly on business to business basis is promising, but we also see the potential of facilitating optimal fortification through governmental means. The approach will be chosen based on the country* where the organization is going to operate.

• Increasing the follow through rate of cage-free pledges*
  
  

Over the last few years, enormous effort has been made to influence the behavior of corporations, and as a consequence, significant effort was made to reduce or eliminate routine confinement practices on factory farms. Strategic, coordinated, and well-executed corporate outreach campaigns seem to be highly promising and cost-effective interventions. Chicken Watch lists 1504 commitments to improve animal welfare by eliminating cage-eggs from the supply chain. However, the ultimate success of such a campaign relies on companies following through and changing the market. There are reasons to be concerned that those commitments might not be fulfilled. Securing the pledges will be one of the biggest challenges that animal advocacy will face in the following years. Some strategies, like the tracking of progress, holding companies accountable, and enforcement campaigns are already in place. To secure follow-through, action needs to be taken on every step of the causal chain leading to the impact for animals. Many of the pledges are hedged with the disclaimer regarding available supply. For example, Walmart's policy states that “by 2025, our goal is to transition to a 100% cage-free egg supply chain, subject to regulatory changes and based on available supply (referring to the farm side production), affordability and customer demand.” Work focused on increasing the available supply is not currently deeply addressed by enforcement campaigns*. This would involve working with producers and targeted financial institutions to facilitate the transition to a cage-free system in the United States. One of the biggest benefits of this charity would derive from the lessons learned from such work. A comprehensive strategy and training could be prepared and shared with organizations globally before implementing it in the country where they are working. This could substantially increase the odds of a smooth global transition to cage-free farming.

• Animal careers - Experiments*
  
  

Many in the animal movement report a challenge in regard to finding the right staff to expand their organization. This problem is particularly present when an organization aims to expand to a new country or when hiring relatively senior staff. There has been relatively little time and attention put into a systematic investigation of what works in hiring and training in the animal movement. It is important to understand the current gaps and carefully test for possible solutions (similar to how Charity Science outreach tested fundraising strategies) in order to have organizations across the animal movement running at their top capacity. Having a focused organization explicitly aimed at animal careers would also give a central selling point for both organizations and candidates to contact for help and advice. Experiments could be conducted in 3 different areas: finding, training, and sorting*. Finding would involve finding candidates who might otherwise not apply for key roles via direct methods, like headhunting, or less direct methodologies, such as reaching out to communities that might have strong applicants but who have not yet considered working in the animal movement. Training could involve paying for possible job candidates to get specific training in a skill area that is lacking in the animal space, for example, management training. Sorting could be largely helped by simply having a central person who knows about all about the currently open job opportunities and can speak to interested activists for 30 minutes and direct them towards the role that would be the best fit. Each of these methodologies could be tested with small scale experiments, with the results and costs being carefully measured to see what works best for getting the key positions filled at top animal organizations.

• Animal research coordination and systematization*
  ​

The research space in the animal movement has grown significantly in the last five years* but there is still relatively little cross-organizational planning and systematic consideration of what research priorities the movement as a whole should have. For example, right now there is a disconnect between what major funders and organizations would most benefit from research-wise and what research is and should be conducted*. Additionally, there is an overlap between different organizations working on similar projects without knowledge of each other’s work. An organization focused on research coordination could create an agenda of research priorities and take into account input from multiple funders, researchers, and implementation organizations. The organization could then work on getting this agenda applied through funding and partnering with other organizations, as well as conducting direct research if no other organization is well-placed or has the necessary capacity (such as RCT research on the most pressing remaining topics). Creating a coherent, well-considered organizational research agenda will take significant time and would likely require yearly updating based on successfully completed research and the changing needs of the movement.
​

Click to see a version with full links

• Tobacco taxation
  ​

There’s strong evidence that increasing tobacco taxation reduces tobacco consumption, and that reduced tobacco consumption results in improved health outcomes. Without increased cessation, tobacco use may account for some 10 million deaths per year by 2030. The WHO estimates that a 10% price increase in tobacco causes a 4% reduction in tobacco consumption. If taxation was changed to the recommended level of 70% of the total sale price in all LMIC, this would result in an estimated 11-27% decrease in smoking mortality and therefore save tens of millions of lives. Numerous pieces of evidence suggest that government implementation of tobacco taxation is highly cost-effective. The Center for Global Development estimates the price of tobacco taxation at $3 - $70 per DALY averted. Copenhagen Consensus estimates a 4000% return, with a $500M/yr tobacco control program averting more than one million deaths annually. Many stated that specifically, tobacco taxation is the most important and most cost-effective portion of the tobacco control campaign. A systematic review of 84 studies also found that taxation was among one of the more effective tobacco control initiatives. The experts we spoke to at tobacco lobbying campaigns and evaluative organizations (e.g., the DCP3) also broadly agreed that this was a strong area to work in. GiveWell is also researching this as a possible area to fund high impact charities in. Although this area has some significant risk of low progress due to working against an intelligent and capable agent (big tobacco), the potential upside makes it one of the most promising and cost-effective interventions possible in the global health and poverty area.

• Conditional cash transfers to increase childhood clinic visits
  
  

Conditional cash transfers (CCTs) entail giving someone a cash incentive for completing a certain activity. CCTs can incentivize behavior that improves well-being while also improving well-being by increasing wealth. GiveDirectly, a GiveWell top charity, has a well-evidenced, high-impact intervention through unconditional cash transfers (UCTs), where money is unconditionally given to some of the world’s poorest people. A CCT seems like it may be able to achieve higher cost-effectiveness than UCTs by successfully incentivizing highly valuable health behaviours while still providing a cash benefit. However, the beneficial effects of the cash transfer may be much lower in a UCT since the ability to target the poorest people is compromised and there are higher infrastructure costs. There are numerous behaviors that could be incentivized and many different incentive sizes and delivery methods. Additionally, it is easy to randomly assign participants to different conditions, including a control condition. This means there is much room to experiment with CCTs, which makes it a flexible, testable and possibly cost-effective intervention class. Specifically, based on our new research* in the area, we think that increasing clinic visit utilization using conditional cash transfers* could be an extremely effective method of increasing the overall health and wealth of a target community. This method could also pair well with other age-compatible high-impact interventions, such as vitamin distribution or deworming.  

​

• Contraceptives*
  
  

Access to contraception is a large issue in many parts of the world, leading to unwanted pregnancies and transmission of diseases, such as HIV. Simple and cost-effective interventions exist to increase access and awareness of different contraceptive methods. Many large funders are interested in this area, and research into new methods and more effective education on the existing methods is on the increase. We believe that working on contraceptive access could be an extremely effective intervention. We are still researching many specific methodologies, including social marketing for condoms, condom distribution and promotion, condom education, video promotion of oral contraceptives, injectables, and long-acting reversible contraceptives and IUD subsidizations. The evidence base for the effectiveness of these interventions is mostly well-understood. Depending on different ethical assumptions, the cost-effectiveness of this intervention could be considerably higher or lower than comparable global poverty interventions.

Did you know that you can now help to start ​an effective charity based on our top ideas? Apply for our incubation program!

When recommending different charities to start in the field of animal advocacy, a crucial question to consider first is which ask should be prioritized? Regardless of the approach - corporate outreach, governmental intervention or individuals focus intervention - we need to decide what we are going to ask them for in the first place. We expect that the ask and a compatible approach have the strongest predictive power on the final cost-effectiveness of a charity. Most approaches rely on conveying a specific ask. For example, when approaching corporations we could solicit for improving the management of dissolved oxygen in fish farms or for optimizing fish feed to contain less fish and more plants. We believe that one is significantly more effective than the other. That being said, there are a many different factors we considered when prioritizing between asks, including:

• Strength of idea

The strength of the idea concerns the cost-effectiveness of an ask, and what weight to put on it given the evidence-base. For example, food fortification looks promising as its evidence base looks strong, which allows us to take its high estimated cost-effectiveness seriously.
 

• Limiting factors

Limiting factors address the most likely factor to limit an intervention from expanding and having an impact. This could be funding, talent, replaceability, size of the problem or logistical factors. For example, ensuring humane slaughter and transportation seems to be a promising idea, however, it’s counterfactual replaceability is limited given that there are already lots of competent organizations working on the issue.
 

• Execution difficulty

Execution difficulty is focused on how hard it would be to apply this intervention in real-world situations, both at the earlier stage of founding and the later stages of execution. It also covers the ability to receive valuable feedback quickly and if the timing is right for executing an intervention in the area. For example, we think the difficulty of doing high impact work in welfare-focused gene modification is extremely high both in the founding, feedback, and execution stage.
​

• Externalities

Externalities cover all non-direct effects both negative and positive of an intervention. For example, many meat reduction campaigns are focused on red meat and might have a much stronger negative effect on small, high priority animals like fish and chickens than any other intervention. This is an externality called the small animal replacement problem.  
​

Did you know that CharityEntrepreneurship can help you start
​an effective charity for animals?
If you want to be the first to know when we will start accepting applications (April 2019) to our incubation program, subscribe to our mailing list. ​

The first month is structured similarly to a full-time university course and includes presentations, guest speakers, activities, and partner projects. The content covered over the first month includes:
​

• Giving and receiving feedback
• Spreadsheets and quantitative decision making
• Task planning and organization
• Introduction to advanced Effective Altruism concepts  
• Early stage management, hiring, and firing
• Charity Entrepreneurship in comparison to other career paths
• Communication skills focused on analytical audiences
• Wellbeing, mental health, and sustainable work output
• Job advertisements, attracting, and retaining talent
• Fundraising, networking, and grant writing
• Independent learning, self motivation, and problem solving
• Research interpretation, synthesis, and acquisition.
• Operational logistics and charity registration
• Budgeting and organizational financial planning
• Testing and determining optimal co-founder fit
• Short- and long-term organizational strategic planning
• Measurement and evaluation and applications in difficult contexts
• Basic statistics and applied informal bayesianism
• Organizational power structures and board management
• Creating cost-effective analyses, interpretation, and program improvement
• Project partners and governmental relations
• Deep comparison of recommend charity ideas.
• When to shut down or scale down your project and when to pivot/Shutting down, scaling down, and pivoting
  
  

In this first month, you will also be given tasks to complete with your classmates. These will be practical tasks, such as setting a budget for a hypothetical start-up. These will allow you to work with all the other people on the course within the first month. This is designed to give a sense of what working with each person is like, helping you to identify potential good fits for a charity co-founder.

At the end of the first month, each attendee will submit a document stating which charity ideas they are interested in working on and who they would be interested in co-founding these with. They will also provide some logistical information, e.g. where they plan to live. Using this information the Charity Entrepreneurship team will come out with a recommendation list of compatible co-founders and ideas. These recommendations will be the best estimate of a high impact team given all the submitted information. Most co-founding groups will comprise of 2 people, but there may be occasions where we recommend a single founder or a group of 3 people.

Some interventions are promising, but not at a stage where founding a specific charity would be the best next step. This could be because an intervention is too young and requires more research before conducting broader, charitable activities. It could also be due to the field being too old, with large players already established and conducting the needed effort in the area. A field that is too old might be a perfect field to fund, and a field that is too young would, generally, be a good field to research without necessarily founding a charity in it. Interventions, of course, can move at different rates, and it's difficult to clearly classify them. However, we do feel some classification of what stage they are at can help to explain why we found some asks to be more or less promising. ​​

• Long term research
• Short term research
• Field establishment
• Growth
• Refinement
• Stabilization
• Decline
  
  

Examples of our ask reports put into different stages:

• Long term research - Gene modification, increasing the price of meat.
• Short term research - Humane insecticides, institutional meat reduction, fish feed optimization, switching consumption from chicken to beef.
• Field establishment - Fish stocking, food fortification, water quality for fish.
• Growth - Slaughter and transportation methods, preventing mutilations.
• Refinement - Cage free campaigns, humane farming promotion, contraceptives.
• Stabilization - Humane farming.
• Decline - Vegetarian outreach individuals, meat reduction individuals, baitfish.

As such, it's not surprising that many of the areas we find most promising are in the field establishment section, with none of the ideas at the very ends of the spectrum matching the most promising ideas. However, if we were looking at the same set of interventions from a funding perspective, we would be mostly looking at “growing, refinement, and stabilization stages”. If we were looking at this list from a research perspective, requiring both long-term and short-term research would be ideal.

The following is a fictional story to illustrate a point.

The two interventions were both urgent. Animal Issues - Canada had been considering which of the two to pick for months. Jeremy thought that they should work on geese, as they had a significantly lower welfare standard than other in Canada. It looked clear to him that they should move the majority of their resources onto campaigns aimed at increasing the welfare of geese. However, his co-director disagreed. Jenny had been researching ducks and thought they were even more important than geese, since the ducks were slightly more numerous, although slightly better treated than the geese. It was a hard call, and so they chose to flip a coin. Both interventions were good, and flipping a coin seemed like a fair way of deciding, but both Executive Directors agreed that whatever the outcome, they would dedicate themselves to the issue.

But the coin betrayed them.

It told them to work on geese, and so they did for years - the two of them were ambitious and talented activists, and thus they made considerable progress. They would have made progress with ducks as well, but they had to choose one. Unfortunately, they had chosen wrong. As they won victories for geese, the goose population was decreasing. Each year, less and less geese were farmed, not because of the activists’ victories, but independent of them. Goose was going out of style - less geese were being farmed everywhere and not just in Canada. And although their improvements had been huge, during the 5 years they had worked on the issue, the goose population had shrunk by almost 50%, meaning that their improvements only affected half as many individuals as they predicted they would.

Duck populations, on the other hand, had exploded, and there were now twice as many ducks as there had been when they had first made the calculation. 5 years later, to their dismay, they compared what would have happened if they had been working on ducks instead of geese, and, sadly, their calculations showed that they could have saved four times as many animals if they had made the same amounts of progress. In some cases, they could not have known which group would grow and which would shrink, but in this case, the data was there and they just had not looked. If they had looked at the trends from the last 5 years before, it would have been clear that ducks were a growing problem and geese were a shrinking one. They had not taken into account the ‘unique timing’. They had not targeted the duck industry when it was young, and now it would be an uphill battle to switch over to a much more established duck farming industry. The solution to this problem was not to invest time and attention by half and half in each. The solution would have been to take a deeper look at the future trends in the farming industry to try to determine what area would have been more important both then and after 5 years.  ​

The graphic shows the change over time of aquaculture production vs the wild capture of fish. It’s clear that aquaculture is gaining market share with wild capture stagnating, and there is good reason to think that this trend will continue with wild capture getting harder as the wild fish supplies are reduced.

This graph suggests that if we want welfare reforms to pass on aquaculture, the sooner the better, because the industry will likely get larger and more established over time. On the flip side, now might be a uniquely bad time to use up resources passing reforms for wild fish, as it’s more likely that the industry will shrink instead of grow going forwards. For example, if you thought the two different welfare interventions “Humane slaughter of fish” and “Increasing dissolved oxygen levels to improve water quality” are about equally important, then the ‘unique timing’ consideration could change your view. An intervention like “Dissolved oxygen” (which generally will be impossible to execute with wild fish, and thus targets aquafarm fish) might look more promising to go forward with right now (it aims to hit before the aquaculture industry gets any larger) than something like slaughter (which targets both wild and aquaculture fish). This would be even more significant a factor for an intervention that just affects wild fish (e.g. bycatch reduction strategies).

Overall, the timing of an intervention should be carefully considered, and interventions that have uniquely good timing should be prioritized over those that do not or those that could be more effectively done at a different time. This is a factor our team is going to consider when recommending new charities. Right now, this would mean targeting countries with low but growing animal production rates, such as Bangladesh, and targeting industry trends like aquaculture.

In this talk from EA Global 2018: London, Joey Savoie, Charity Entrepreneurship's director, discusses why charity entrepreneurship is one of the highest-impact things you can do. He also explains what we can do to help you start an effective organization.
Below you can find the full video and a transcript crossposted from effectivealtruism.org prepared and lightly edited by The Centre for Effective Altruism (huge thanks for their hard work).

You can share your thoughts about this talk on the EA Forum.

Of course, India is not the only country with problems, and of course, global poverty isn't the only problem. There's tons of different issues that one can work on, like animal welfare, mental health challenges, economic development, or migration. There are a lot of gaps in the world where new and effective organizations could be founded.
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Why I'm talking about these gaps is because I think that a lot of people are under the impression that there's already a ton of charities out there. Maybe all the best opportunities have been filled by organizations, and that's really not the case. There really is room for fantastic new charities to be founded and be fantastically high impact.

I'm going to make this argument from more of a cluster thinking perspective than a sequence thinking perspective, which means coming at it from a bunch of different angles and showing that charity entrepreneurship looks very good and very high impact from several different perspectives.
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The first thing that comes to almost everyone's mind when they think about the potential impact of charity entrepreneurship, is the sheer size of good that you can do when you found a successful charity.

Here's some of the money moved from some top GiveWell recommended charities. You can see it's often in the 10s of millions of dollars. And these are just the numbers from GiveWell itself, as opposed to the total money that's going towards each charity.

Suffice to say that starting a high-impact charity can redirect millions of dollars in a positive direction. So, even if your charity is only 1% more effective than the charity that a donor would have given to otherwise, it can have a really massive impact just because of the sheer volume of money.

There's also a force multiplication argument about this. You're not just directing money, when you're founding a new charity. You're directing talent, you're directing interest, you're directing passion towards your chosen issue. There are a lot of people who will work for a high-impact charity, but wouldn't ever found one themselves. By creating a new high-impact charity, you're creating an opportunity for talented individuals to get invested in the field and to make a difference.
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Finally, there are hits. So, everyone wants their charity to be successful, and charity entrepreneurship is inherently, like normal entrepreneurship, a risky business. A lot of charities will be started and the impact analysis will come back bad, or the charity won't have a valid way of scaling. There's a lot of ways to fail, but there's also a lot of ways to have massive success. Success that is incomparable to many other jobs. For example, a minor hit, although it feels funny to call it a minor hit, would be becoming a GiveWell recommended charity. Just a small percentage difference between you and the other GiveWell recommended charities in terms of being better, or even simply giving more options that GiveWell can recommend to attract donors from different spaces and different interests. So a minor hit can make a huge difference.

But that's not even taking into account the major hits. Most giant charitable organizations that are around today started off as a small group. The benefits of an EA group being the group to start the next Oxfam, and shaping an entire cause area, is truly massive.

The next thing we'll talk about is tractability and track record. Founding a charity is a difficult job, especially one good enough to be a GiveWell or Animal Charity Evaluators recommended charity, but it's not impossible. Some of our collective track record shows this. A lot of the charities we view as strongest and most impactful in the EA movement, weren't started by someone with 55 years of experience in the relevant area. They were instead started by someone who came into it with more of an analytical mindset, more of an EA mindset, someone looking for cost effectiveness or evidence base.
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A lot of the recent charities that have been started and that have become GiveWell incubated, were coming with the same mindset. That's a huge competitive advantage over other charities that happened to be cost-effective by luck, as opposed to explicitly seeking cost-effectiveness out or trying to maximize it.

No good EA presentation would be complete without an expected value calculation. So what's the numerical worth of Charity Entrepreneurship? Well, there are a couple different calculations. Peter Hurford's calculation assumes an 85% chance that the charity has zero impact, so fails completely, and assumes a 15% chance of becoming GiveWell recommended. These numbers were based off Charity Science Health, the charity that we founded, after doing a similar round of analytical research to the ones that we now do for all sorts of charities.

His model determined that the average staff member would be worth $400,000 of equivalent donations to high impact charity. That's just the average staff member, that wasn't for co-founders or the founding team in particular. This is an incredibly high impact thing. This is $400,000 donated. So, even if you earned $400,000 you'd have to donate 100% of it to match this level of impact. We did an internal model that was a bit more pessimistic, assuming that there's only a certain chance that someone would get to the point where Charity Science Health has got, and get GiveWell incubated, and ended up at a similar figure of $200,000 of expected value of donations.

This sort of impact is really, really high, and these calculations are quite conservative relative to a lot of the other impact estimates going around the EA movement.

There's a whole bunch of other benefits that I'd love to spend more time on. But I'm going to go through really quickly because we only have so much time. The first one is skill building. So, entrepreneurship gives you an opportunity to try on a lot of different hats. That's part of why it's hard and intimidating, but it also gives you a chance to build a lot of different skills. If you try to found a charity, even if you fail, going into the next job having basic budgeting skills, fundraising skills, management skills, hiring skills, it gives you a huge advantage and will stick with you for a long time.

Similarly, career capital. If someone sees that you took a good attempt at a project, even if it's a failed project, but especially if it's successful project, that does wonders for your CV and career capital in general. You can use a successful charity as a stepping stone towards getting into a high impact position with the World Health Organization, or any sort of other organization that would look at that sort of thing.

The next thing is attributable impact. So, calculating the impact that you're going to have is really, really difficult, and there's one less step you have to calculate with charity entrepreneurship. If you do, in fact, start a charity that no one else would have founded, that wouldn't have gotten started without your time and energy put into it, what you're most looking at is that charity's impact as a whole. Instead of having to calculate both the organization's impact, and then your specific impact within the organization. When calculating your impact in othre cases, maybe the organization is great, but your personal role is very minor. Or maybe your staff impact is big, but the organization sucks. With charity entrepreneurship, you only have to calculate the organization's impact.

Job satisfaction is the next one. As I said, it's really not the perfect fit for everybody, and we'll go a little bit more into that soon. But for the right personality type, it's incredibly enjoyable. Being able to look at your charity and know that you built it from scratch, being able to work with flexible hours, with a bunch of different staff. There are a lot of benefits to it. There's an unparalleled amount of job diversity. But there are also cons. Ambiguity is tough, which is a thing you're going to have to deal with as a charity entrepreneur.
Not only are there personal benefits for founders, there are also benefits to the EA movement in general. Charity entrepreneurship enhances movement growth, by expanding the EA movement outside of its traditional sphere. By getting involved at the charity level and hiring people in that field, working with people who, say, work in vaccinations, you expand EA in a very concrete way to a sympathetic audience.

There's also a much clearer case for impact for some of these charities. It's fine to go and tell someone that you're doing a philosophy think tank that will eventually save humanity, but it sure is nice to also be able to say we started a vaccine charity that people think is highly cost effective. That sort of concrete case for impact can benefit the whole EA movement, in terms of showing that we are in fact doing what we say we're doing and having success doing that.

The next thing is stability. Organizations tend to outlive movements. The EA movement is social movement, and it is fragile in many ways. It gets stronger the more organizations there are to anchor it, and tie it to reality in a long lasting way.

Finally, opportunities. Lots of EAs want to work for EA organizations. Lots of EAs wants to work for high impact jobs. As I mentioned with the force multiplier before, by creating an opportunity, you create space for people to grow, develop their capacities, and expand the EAmovement. It gives a space for people to go once they get involved.

Next up, community learning value. Even a failed project can be massively impactful if you get a lot of learning value from it. One of our early projects didn't work at all, but we were able to publish a giant report explaining why it didn't work and tens of other organizations in the EAmovement were able to learn from that mistake and not repeat the same thing. If your charity does fail, and you are able to be transparent about why it failed, and you learn from it, you can benefit not only the charity entrepreneurship community within EA, but the broader EAmovement as a whole, because a lot of these lessons are generalizable.

Finally, there's inspiration. If you can inspire someone else to found a charity through your example, that can be massively high impact. If people can see other people doing successful, ambitious projects, then it can lead to precedence. So for instance, we saw New Incentives do a really great job founding their charity, and that gave us confidence to start Charity Science Health. Charity Science Health gave Fortify Health confidence to do that, and now Fortify Health, New Incentives and Charity Science Health can give other EAs a chance to look at charities that have been successful and it gives them a chance to feel inspired by the possibility.

The next thing is passive impact. So, for people who have heard of passive income, passive impact is a very similar concept. Basically, if you set up a charity to run independently without you, and it continues to do good in the world, you continue to hold some sort of counterfactual responsibility for that impact.

​The last thing that I'll talk about briefly is just the room for more funding. Room for more funding isn't a huge impact if it's filled by someone who's otherwise going to donate to a fantastic charity, but by creating a new charity, you can leave a lot of room for new donors to get involved, and donate to maybe something particular to their interest, while still making a really high impact.

So why now? There's a lot of reasons why founding a charity now in particular is maybe a lot better than historically. Hopefully, it will continue to be this good in the future. There's a lot of funder support and funder interest in this sort of thing. The GiveWell incubation program has been trying to fund programs that might eventually become GiveWell top charities. Animal Charity Evaluators has money for this, Open Philanthropy is very interested in new charities and of course, Charity Science, my organization, provides seed funding to new projects starting up. Just an unparalleled time where funding probably won't be the major bottleneck for a lot of charities being founded, if they are founded in an evidence-based way in an evidence-based cause.

There's also mentorship support. You're not the first charity working on this anymore. So you are able to kind of connect with an alumni community. Charities that we've talked to have shared hiring pools and strategies for management and all sorts of different things. The EAcommunity really is starting to build up a network of people you could talk to about issues, whether it's communications or research, and really get an informed perspective of someone who's done something quite similar, quite recently.
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Finally, there's still gaps. That's why I talked about one specific case at the beginning. It's really, really easy to forget just how big the world is, and just how large-scale our problems are. There's a ton of malaria charities, and yet, there's still malaria, killing hundreds of thousands of people every year. There's still a lot of work to be done, and the EA movement can contribute a lot more to that. Specifically, there are even lists of ideas that people would like to see more of. GiveWell has a list of priority programs that has 25 ideas. ACE has a list of charities that it would like to see, with 17 ideas. Charity Science Entrepreneurship, we want to do a research program that recommends two to five ideas every single year, that'll be particularly promising to found, in the GiveWell priority program ballpark, or even more high impact, like something that could compete with AMF.

Okay, so first up, personality. This is an example of a fantastic charity entrepreneur. I'm not talking about Prince William; I don't really have an opinion on whether he can make a good charity entrepreneur or not. I haven't spoken to him personally. But I have spoken to Rob Mather. He really embodies what a fantastic charity entrepreneur might look like. One of the things I want to highlight about him is his personality. Personality is so key, when it comes to charity entrepreneurship. It's one of the first things we look for in our vetting process, and one of the things that I think determines eventually whether your charity ends up being massively high impact or not.

You need a lot of different things. You need to be resilient. There are going to be bad days, bad weeks, and potentially even bad months where you think your charity is low impact, that it wasn't worth founding, and that it's too hard to get yourself motivated. And as the founder, you have to motivate not only yourself, but also your co-founder and your employees. You have to be ready to take those shocks and keep moving on, keep moving through them even when it's tough.

The next thing is being ambitiously altruistic. So a lot of entrepreneurs love ambition. It's a very common thing, but it's really easy to be ambitious about the wrong thing. If you're ambitious about how big your charity is, your charity might get really big, but it won't necessarily do any good. What you need to be ambitious about is how many lives you save, or whatever your end line metric is for doing good. That's the thing you have to be laser focused and truly ambitious about.

​The next thing is results oriented. Quantified measurement is one of the things that makes EAdifferent from many other movements. We really want to see concrete, specific results, and have data to back it up. Staying focused on this will stop your charity from diverging into 100 other projects that might not be as high impact, and it really can make a difference in the long term.

The next thing is being open-minded. You won't have all the skills you need. Nobody does, when they first found a charity. You have to be able to update based on the world changing, based on testing out one thing and it not working, based on advice from people in the field, people who have worked in specific areas that you don't have knowledge in. You have to be ready to amalgamate all these different views, and come up with a coherent answer, and update as new data comes in.

Similarly, it's important not to be afraid to make mistakes. You will make mistakes. Every charity entrepreneur does, and will. Being able to admit these mistakes transparently, learn from these mistakes, and update them can be the difference between your charity eventually succeeding, and you continuing to make the same mistakes again and again.

Next, self-motivated. This might be the most important criterion. You really have no boss, no person whipping you at the end of the day to get the work done. You have to really care about your charity and be able to put in the hours, to be able to work yourself through the project. One of the easiest kind of litmus tests I have for charity entrepreneurship fit is, can you get yourself through a self-directed project? Can you complete an online course without anyone needing you to? Can you start something where only you're responsible if it succeeds or fails? That sort of thing is really challenging for a lot of people, and it's really, really challenging to do a charity like this. You will have your co-founder, you will have your mentors, you will even have funders you have to report to, but not at the same level of regularity that any other job will make you. You have to be self-motivated.

Creativity also helps. There will be a blank slate. You won't necessarily know what the next steps are, and you have to come up with ideas. How to test one thing, how to test another thing. If you come up with five ideas, five ways to test a given concept, that's the limit of how good you can get: the best of five. If you come up with 30 ideas, you can test them all, you can evaluate them all, and come to the best of 30. That makes a huge difference for your charity's impact.

Next, doing it for the right reasons. This is a bit different than being ambitiously altruistic. You really, really have to be focused on doing good for the world. If your goals are different, if your goals are divergent and you want to create a charity to look good, or to impress a partner, or something like that, your charity won't end up being high impact. You really have to be laser focused on that, doing it for the right reasons, with an altruistic mentality.

There are some other things it helps to have. It's nice to be highly competent, whatever that means. Kind of general ability, conscientiousness, IQ, that sort of thing. The EA community is a huge asset, a bunch of skillsets that you can tap to, a bunch of people who really want to help you start a charity. Social skills or research skills, it's really great to have one of those. Your co-founder can balance you out and have the other one. And experience working in a small organization charity can give you a sense of what it looks like from the inside. You tend to think that every organization is perfect, and when you get on the inside, you tend to see how held together with glue and tape it really is.

What's less important than people generally think? Well, one is a degree. A lot of people think that if they want to start a global health charity that's fantastic, they need to get a global health PhD. Unfortunately, those programs end up being too unspecific a lot of the time. For my charity, SMS Vaccine Reminders, you might have only read a page or paragraph in a global health program about this sort of intervention. It's just very, very specific, not to mention the country context. What you need to be able to do is become an expert, it's not necessarily through a degree; it's through reading the studies, reading the research, getting very, very expertised in the very narrow domain that you want to start a charity in. You want to be able to talk to experts and engage with them at the highest possible level, but you won't get there from doing a PhD program. You'll have to do the independent learning on top of that, in either case.
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Also, targeted experience. At a health nonprofit, you might be able to pick up some good habits, but often your role will be very specific. If you're working for a large, even a well run health organization, often you'll be running one very small component of it, whether that's a comms job or a research role. That will give you some skills in that area, but as a charity entrepreneur, you really will need to learn a little bit of how to do everything. Some people might come into charity entrepreneurship with five out of 100 skills that they need, and other people might come in with nine out of 100 skills that they need. Either way, you still need to be able to develop 91 skills. A lot of it comes down to being able to learn things on the fly, try things out, pivot and update based off evidence, talk to mentors and utilize their skills. That sort of thing is going to be far more important than coming in with a few extra skills.

Next thing is, connections in the field. Connections in the field are super important, and you do need them to have a successful charity. But you'd be amazed how willing these people are to talk to you. If you come in informed and keen, and with some expertise or some funding, a lot of these organizations are extremely excited to talk to a young or experienced person who's getting involved. They want to see other charities. They care about this stuff a lot. And they're not getting a thousand emails a day, if they're running some small program out of India.
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In general, it's a very, very easy to build the network, and that is how you build the network, by working in the field. It's helpful to reach out these people and have a quick Skype with them, tell them what you're doing, tell them what you're considering, ask them for advice. Everyone's been very happy to help when we've done this on multiple different projects, across multiple different cause areas. The one exception to this is government connections. It's hard to build government connections; they're not willing to talk to you. If you're doing a job where you need government connections, hire someone who has the government connections. That's the advice there.

So, a little bit about further testing. The best way to test if you're a great fit for charity entrepreneurship in the way I'm talking about it, might be applying for our incubation program. I'll talk a little bit more about what that offers and why you might consider it, but we do have a process that we've used before, on entrepreneurs, that has been fairly successful at selecting the kind of people who might start a GiveWell incubated charity.

We have a quiz on our website. It's a lot less intensive than doing the full incubation program process. It's pretty quick, about three minutes, and it will give you a sense from a personal perspective if you might be a decent fit or not for charity entrepreneurship.

Finally, generally on our website we're trying to put out as much information as possible. So people can self-select, people can consider whether they're going to be a good fit for charity entrepreneurship or not. Our mail list, we send out of all of our relevant research as well as like, helpful things like Facebook group links, to ways that you can ask people questions, and all that sort of thing. So that also can help to give you a sense slowly of whether this might be a good fit as a career path or a bad fit.
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In general, though, don't be too discouraged. A lot of the strongest charity entrepreneurs I've talked to are scared, they're nervous, they're not the archetype of a gung ho, confident entrepreneur. Some of them are cautious. Some of them are detail-oriented, some of them are not gregarious. Don't let superficial entrepreneurship associated traits fool you. Instead, try to get as good as sense as you can from external people who have looked at it before, or by talking about it, or by reading the content from people who have started successful charities.

Here are a few of them in particular. Tobacco taxation looks fantastically cost effective if you can get the right country. Conditional cash transfers have a case for very strong impact, and are being done almost nowhere by NGOs. This year, we're going to be focusing on animal interventions, and researching that, and looking for the highest possible impact interventions that one could start in the field. We're doing research a bit different than say, GiveWell, or Animal Charity Evaluators. We're looking for gaps, areas that could be really promising, could be really effective, but don't have anyone working in them necessarily.

​Malaria is a fantastic place to work, but AMF is doing a really good job, I wouldn't want someone to start another bed net charity. But there are areas that are both fantastically high impact and neglected, as in no one's working in the kind of way that we as effective altruists, or we as people who want help the world, would like to see it done.

So the incubation program that we're running is taking place from June 15th to August 15th, and we'll be hoping to run it every year. We really want to make the process of founding a charity as easy as possible. So we're giving structured support that slowly withdraws, until people are fully independent and standing on their own two feet. The first month will be something akin to a university class. There'll be activities, there'll be pairing with different co-founders to test out your abilities in different ways, there'll be explicit teaching about cost effectiveness, or fundraising plans, all the hard skills that you might need to run a really good charity.

The second month, you'll be paired with co-founders on an idea and start working on a project, but with a lot of support from teams of people who have already successfully founded charities. Finally, over the next six months, you'll be given a seed grant, to financially support yourself so that you can really become a true domain expert before seeking external funding. Seed grants are about $50,000, depending on how many charities apply.

This structure allows someone who maybe doesn't have a ton of experience in working for NGOs, or nonprofits, but is able to build the experience as they go and get really competent and capable, to start a high impact charity.
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We really don't want it to just end after the seed grant ends, we want to continue to support charities as long as they need it. We're trying to build a community such that people can continue to stay connected, whether that's over Skype or Facebook, or a co-working office that we're going to have. We want to have joint office space so that people can feel like they're working with a team instead of working alone or with their co-founder. The seed grants I already mentioned. We'll also connect people with long-term funders. We don't want to see these charities just run for six months, and then flounder. Most of the connections will be people who are very keen on founding new charities, and ongoing mentorship.

So I still continue to Skype with the projects that we've helped, and help them with the most difficult issues, so they can have an external set of eyes for as long as they need it.

Question: Earlier, one of our speakers, Dr. Glennerster, said that she really advises young people to make sure that they spend some time in an effective organization so they know what an effective organization looks like. What do you think about that?
Joey: Yeah, it helps a lot. When people ask me what they should do if they're still working on their degree or are looking for internships, I always say, prioritize how good the organization is. It doesn't have to necessarily be in a tightly related area, but if you work for a charity like AMF, or pick up some of their management practices, that's going to be one of the best things you can do to set yourself up to run a charity really well.
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Question: It seems like the charity space has a proliferation problem, where there are lots of small charities, often nipping at different corners of the same bigger problems. What's your take on that, and how do you think about people joining versus starting charities given that reality?
Joey: So, we're pretty pro starting versus joining. Joining organizations, whether they're small or big, it's incredibly hard to change them in an effective direction. You can ask a lot of people who have worked with these organizations to get a sense of that. There are lots of charities, but most of them are incredibly small. You'll see a statistic like there's a million charities, but almost all of them have an operating budget of under $50,000 or something like that. So it's not like they're taking out huge chunks of global problems. What you really have to look at is the scale of the remaining problem, and whether you can start a charity that starts to cover some of that problem.

We will provide both formal and informal mentorship opportunities to all our incubated charities. All our charities will be invited to join in on 3 weekly one-on-ones (over skype calls if the charity is founded in a different location). One will be with a member of our CE team who has started a charity before; another will be with one of our alumni charities, who have started their charity in the previous few years; and the final one will be with other charities started in the same incubation round as you (your classmates from the program). These calls are designed to help you gain insight and advice for the next step of making your charity successful. There will also be a Slack channel for you to share thoughts with the community and get in contact with specific people. ​

Did you know that CharityEntrepreneurship can help you start
​an effective charity for animals?
If you want to be the first to know when we will start accepting applications to our incubation program, subscribe to our mailing list. ​

The problem size limit is indeed huge. In fact, it has to be cropped, or otherwise it would go all the way to the top of this post and the other sections would become impossible to see. However, that is not really what matters. Even if wild animal suffering is a huge problem and even if there is only a very limited amount of funding and talent that wants to work in the area, you will bump into problems with scaling far before it starts to matter if there are a billion wild animals or a billion billion. In the practical cases, when comparing these interventions, if a charity were founded in both of these areas, the vaccination charity would be able to get to a much larger scale than the wild animal suffering-focused charity could. A claim that “we should work on intervention X due to its massive problem scale” seems quite inaccurate. These sorts of arguments are extremely common for wild animals specifically and more broadly in EA.

Researching to determine the causes’ limiting factors generally ends up with more time being spent on considering the funder and talent space compared to, for example, mapping out the specific number of animals affected by any given intervention. And it usually ends up with a set of fairly different interventions looking promising.

Of course, the perspective changes depending on what you are looking to do in a given area. For example, when considering donating to a charity, the main thing examined by Givewell is room for funding. They are looking for an intervention for which its limiting factor to doing more good is funding. Some interventions might be very promising, but due to talent, logistical problems, or the size of the problem limitations, even if Givewell gave them more funding, they would not necessarily be able to create more impact. Organizations with room for more funding are generally stopped not by other factors but by ‘room for funding’ itself. Due to Givewell being a funder, it makes sense for them to take a careful look at room for funding as that is the limiting factor they can improve. As a charity entrepreneur, what the funding space looks like for a given organization should play a big role in what charity to found. As an employee at an NGO, you mostly have to consider how much of a limiting factor talent is for the organization.

These models are really simplified on both the scale and the limiting factor side, and I think there are other possible ways to use scale differently (or use tractability in a different way to cover some of the same concerns). I do not think 100% of EAs use a simple scale-based way of looking at problems, but I do think a large % of EAs use a fairly simple “size of the problem” based way of considering scale without thought to the % of the problem they can solve, given the first limiting factor that will stop growth/progress.