Some important research questions in economics

Disclaimer: This list is heavily influenced by my own research and thus only a tiny subset of important questions in economics and adjacent areas is presented.

I met a young economist at EAGx Berlin who considered switching to AI Safety research because of the apparent lack of impactful research questions in economics. The young economist was under the impression that the case for working on AI Safety is crystal-clear and that there are no important questions in economics. I believe that there are many different problems in economics that can be tractably solved with additional research. You can imagine the conversation as follows:

Young Economist: “AI Safety seems important.”

Me: “Sure, but there are tons of great research questions in economics too.”

Young Economist: “Like what?”

Me: “Well, there is growth, this is super important you know… and a bunch of other things… really, sooo much I do not even know where to start.”

I was unable to provide the young economist with a set of important questions from the top of my head. Therefore, I decided to make this list.

It is not a well-curated research agenda. To have that would require that many share their knowledge.^[1]

I have only listed questions that can be addressed by anyone with some quantitative skills and basic economics knowledge. Every research question comes with an angle-of-attack in the footnotes. Most research does not even require genius, but simply labor.

Forecasting

Can we make use of ‘subjective truth serums’ to inform policy decisions and make better long-term forecasts?^[2]
Is long-term forecasting distinctly different from short-term forecasting? How to best produce long-term forecasts? What can be robustly said about the latter given the current track record? ^[3]
Can Full-Accuracy Scoring improve relevant mid-term and long-term forecasts? ^[4]
How to forecast AI Progress and technological change? ^[5]
How to communicate forecasts to policy-makers?^[6]
Is there a fundamental estimate of individual predictive skill, such as the Elo rating in chess? ^[7]
Awards in (forecasting) competitions are only handed out to a small number of forecasters- are forecasts measurably skewed? How to align incentives? ^[8]
Forecasts on events should be biased in favor of an early outcome unless this bias is actively counteracted if forecasters prefer to reap rewards earlier rather than later. This is an important consideration for making robust mid and long-term forecasts. Is this bias observable in practice? ^[9]
Assuming a situation in which a forecast affects behavior: Is the forecaster endowed with a decision or power in such a situation? What is the (moral) role of the forecaster in such a situation? For example: Better predictions for economic crisis seem useful, but a potential downside is that predicting a crisis may alter behavior in such a way that it leads directly to a crisis.^[10]
Assuming that future generations further adapt to their economic, socially and cultural environment, they will be very different from us, just as we are extremely different from the society of 1924. Can we forecast such social changes? ^[11]
How can we best estimate the outcomes of studies that are not yet carried out? ^[12]
How can we best nowcast pandemics? ^[13]

Futures

I think there might be a lot of value in exploring concrete scenarios. It is important to notice that whilst that particular scenario is extremely unlikely to ever occur, its analysis may discover nonintuitive repercussions and could meaningfully inform our understanding of similar scenarios and is thus useful. The method is simple: Assume a baseline future scenario but make exactly one change to it. Then use our understanding from multiple disciplines to find out what such a future might look like. ^[14]

A couple of obvious candidates would be:

Catastrophic Climate Change
Transformative Artificial intelligence
Supervolcano eruption
Nuclear winter
Large drops in fertility/willingness to have kids
The US or a major western country becoming authoritarian
Cheap autonomous weaponry
Very advanced synthetic biology (and engineered pandemics)
Countries building out solar geoengineering capabilities
Extremely large economic crisis—I am talking (The Great Depression) $^{2}$

One would have to be very specific about the change that is introduced. Such a project would likely take book-form and multiple years of research, so it is ideally suited for interdisciplinary PhDs.

Climate Change

The amount of research regarding climate change is vast and growing. However, given the gravity and complexity of the situation, much seems to be missing yet:

How do long-term energy forecasts of statisticians, economists and geoscientists compare? Help forecast the adoption of different energy sources. ^[15]
How could we improve upon existing climate agreements? Which key assumptions or agents make (future) climate agreements work? ^[16]
Can central banks help mitigate climate change? Should central banks do so? ^[17]
How do geoengineering methods play into future climate coordinations?^[18]

International relations

How can international agreements improve upon pandemic response? ^[19]
How will (military) technological progress, such as the cheap availability of autonomous or biological weapons, change international relations and the future of warfare? ^[20]
How successful have attempts to forecast war been? ^[21]
Is it possible to get enforcable international agreements? ^[22]

Macroeconomics & Economic Growth

Help us understand economic growth and technological progress better. What will future economic growth be and how can we shape it? ^[23]
If technological progress is so “fast” right now, why the low growth? ^[24]
How should financial markets be regulated? What are the effects of regulation on financial stability? ^[25]
What should we expect a non-economic growth world to look like? ^[26]
How should we expect TAI to influence economic growth? ^[27]
What can be said about an economy with “fast take-off”, i.e. where a substantial additional tasks can be performed cheaply by purchasing additional computational power? ^[28]
Can central banks help alleviate pressing problems not directly related to economic crisis? ^[29]

Many issues concerning growth and macroeconomic policy intersect with other areas.

Public Choice and Democracy

Why are countries currently autocratizing? ^[30]
Forecast democratic trends—What does history tell us about our future of democracy? ^[31]
How to implement better voting methods? ^[32]
How, why and when are existing policies revised? Is there less willingness to get rid of old policies than to create new ones? ^[33]
What is the effect of longevity on autocracy? ^[34]

Development Economics

Important open questions in Development Economics seem to be abundant. Thus, I give some examples rather than concrete research suggestions: A recent study investigated the ‘spillover effects’ from GiveDirectly donations in Kenya. This study has likely been a big update on the effectiveness of GiveDirectly and has informed our understanding of spillover and multiplier effects as a result of increased spending. The study is, on average, cited twice per week (extremely influential) and could have easily been available five years earlier. Many philantropic organizations (such as GiveWell) seem to draw most of their evidence from studies in Development Economics.

Open Philanthropy has recently published which type of research they think would be very helpful for them.

Another recent study provides evidence on how to discover promising grantees for entrepreneurial microgrants in the developing world. The study suggests that returns to cash givings could be tripled by letting the local community predict entrepreneurial success.

Studies in developing countries inform cost-effectiveness estimates of micro-interventions, such as deworming children or giving cash to the poorest. However, macro-interventions that promote economic growth and organization throughout an entire nation might be far more cost-effective. Unfortunately, it is much more difficult to figure out whether macro-interventions, such as promoting open markets or educational reform actually work well. You cannot run randomized trials with entire countries. Given the importance of such questions, it is likely worthwhile to tackle these questions.

This study also informs grant-making. This and this recent forum post as well as the questions on economic growth might also be interesting.

The post by Open Philanthropy also suggest that they also consider immigration policy to be a important area of future research. Given that the effects of immigration seem to be dependent on a large range of factors (the immigrants, number of immigrants, how they are integrated) studying the contemporary effects of immigration in key countries is highly interesting.

Study (Effective) Altruism and relevant social groups

Studying the EA community and other relevant social groups itself may be very valuable. Furthermore, there are many questions highly related to giving and spending that can potentially be answered by additional research. Some potential research questions are:

How to increase the funds directed towards effective charities? ^[35]
What are causes of peoples engagement with (effective) altruism? Why is effective altruism a recent phenomena? ^[36]
How can incentives in academia be changed so as to improve the quality of scientific work (as e.g. has been demonstrated with registered reports)? Which actions can be undertaken that steer academia towards better incentives? ^[37]

Philanthropic spending across time

How should a philanthropic actor spend resources across time to maximize utility? ^[38]
How should we discount the future? ^[39]
Which behavior should we expect to see, if there is mainstream concern that there is a high risk of disaster? What is the interplay between personal discounting and financial market interest rates? ^[40]

Other

Should factory farming be taxed? What would the consequences be? ^[41]
Can mainstream perception of catastrophic risk lead to broad value-change? What would be the implication of that? ^[42]
Theoretical Economists may bring to bear interesting results in AI. After all, economics studies rational agents, and AIs should therefore be even more predictable than humans.
Can we study large language models to learn about human behavior? Are results from social science experiments with large language models closely representative of experiments with human subjects? ^[43]
Can large language models be used to more rigorously analyze text output of human subject in social science experiments, providing the opportunity for unbounded long-form answers as opposed to survey tickboxes? ^[44]
Can the different theories of causal inference be reconciled?^[45]
Can Pearls SCM framework be extended to incorporate cyclical causality? If yes, how?^[46]
Review the economics of the catholic church. Why is the institution so robust to change? ^[47]

Another source of inspiration may be research agendas of others:

GPI Research Agenda
Research Agenda on AI & Economics (Work in progress)
80000Hours curated important research questions
Long list of AI question (related via Forecasting and Theoretical Economics)
Charlotte Siegmanns Research Agenda on AI Risk and Economics
Social science research we’d like to see on global health and wellbeing [Open Philanthropy]

Do you know of important questions + angles-of-attack that you would like to share? I will add your comment with your name to this list!

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In some ways, this is an economics problem of its own.
It is very difficult for an individual researcher to actually know which research will have important consequences. This is well represented via the fact that individual researchers are poor at predicting which studies replicate, and what the outcome of studies will be. However, a crowd of researchers is able to distinguish a study that will replicate from a study that won’t.
DellaVigna, S., Pope, D., & Vivalt, E. (2019). Predict science to improve science. Science, 366(6464), 428-429.
See also: Hanson, R. (1995). Could gambling save science? Encouraging an honest consensus.
Thus, I would like to see a venue where researchers share their ideas and rate others ideas. This would be complicated to install in a robust way. Yet, it is not impossible at all. The game changer would be if researchers could gain prestige by suggesting research ideas that will be considered great by others. This could be implemented in a bi-annual survey or something similar.
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This question is from the GPI Research Agenda.

Researchers have developed sophisticated methods for belief elicitation when ground truth is not available to the experimenter/principal who is interested in the forecast. See e.g.:

Prelec, D. (2004). A Bayesian truth serum for subjective data. Science, 306(5695), 462-466.

Weaver, R., & Prelec, D. (2013). Creating truth-telling incentives with the Bayesian truth serum. Journal of Marketing Research, 50(3), 289-302.

Currently, long-term forecasts and other non-verifiable estimates are being produced via the time-tested method of “just asking”. How well these methods work for important applications such as estimates of the effects of policy interventions or philanthropic interventions or long-term forecasts is not known. This can be found out via additional theoretical and empirical research. I am currently working on a review paper that outlines exactly which additional research is necessary and why that is. Reach out to me directly if you want to know more.
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This question is from the “Forecasting AI Progress research agenda”.
See e.g.: Craig, Paul P., Ashok Gadgil, and Jonathan G. Koomey. “What can history teach us? A retrospective examination of long-term energy forecasts for the United States.” Annual Review of Energy and the Environment 27.1 (2002): 83-118.

A good start would be to build a more exhaustive track-record of long-term predictions. This is difficult given that such predictions are often packaged in text and may not be stated in probabilistic terms.

There is some literature on the topic available. The most important step would perhaps be to make a literature review.

Also:

Christensen, P., Gillingham, K., & Nordhaus, W. (2018). Uncertainty in forecasts of long-run economic growth. Proceedings of the National Academy of Sciences, 115(21), 5409-5414.

Müller, U. K., & Watson, M. W. (2016). Measuring uncertainty about long-run predictions. Review of Economic Studies, 83(4), 1711-1740
Tetlock, P. E., Karvetski, C., Satopää, V. A., & Chen, K. (2023). Long‐range subjective‐probability forecasts of slow‐motion variables in world politics: Exploring limits on expert judgment. Futures & Foresight Science, e157.
Granger, C. W., & Jeon, Y. (2007). Long-term forecasting and evaluation. International journal of forecasting, 23(4), 539-551.
Kott, A., & Perconti, P. (2018). Long-term forecasts of military technologies for a 20–30 year horizon: An empirical assessment of accuracy. Technological Forecasting and Social Change, 137, 272-279.
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Full-Accuracy Scoring is a recently and decently researched method that combines forecasts based on 1) the past track record of forecasters and 2) how the forecasts made on not-yet-resolved questions compare to the aggregated prediction (serving as a proxy for the outcome).

Thus, the method leverages information on forecasting accuracy from the past and “future”—hence the name.

The method looks particularly promising for situations where there are both near-term, mid-term and long-term forecasts. A first testbed could be the AI Progress and the Our World in Data Metaculus tournaments. Does the method improve upon the forecasts there? Are long run predictions under Full-Accuracy Scoring very different from other aggregated predictions?

The paper:
Atanasov, P. D., Karger, E., & Tetlock, P. (2023). Full Accuracy Scoring Accelerates the Discovery of Skilled Forecasters. Available at SSRN 4357367.
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Big question!

Too big to tackle as a single research question. There is a research agenda for this that suggests some concrete research questions:

See: Gruetzemacher, Ross, et al. “Forecasting AI progress: A research agenda.” Technological Forecasting and Social Change 170 (2021): 120909.

Given the rapid progress in AI research, it would surely be interesting to make a literature review here too.
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One could study in a randomized trial how politicians respond to forecasts that are identical, but are communicated in different ways. From that we would be able to learn how to present forecasts so that they are easy to comprehend.

In my experience, politicians (even those on a very high level) are very talkative and ready to devote time to matters as long as this may be linked to political beliefs. I think it would be best to target politicians that barely missed the opportunity to become representatives at a state or national level.
See e.g.:

Fischhoff, Baruch. “What forecasts (seem to) mean.” International Journal of Forecasting 10.3 (1994): 387-403.

Doyle, Emma EH, et al. “Communicating likelihoods and probabilities in forecasts of volcanic eruptions.” Journal of Volcanology and Geothermal Research 272 (2014): 1-15.
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I think there is. I am working on this right now so contact me in case you are interested.

Why is this important? An estimate of skill or ability to forecast the future is clearly what we are interested. Currently, we are focused on accuracy. Accuracy however depends on the difficulty of the question. Thus, it tells you nothing about forecasting skill just as the track record of a chess player tells you nothing about their skill. You also need to know who they have played against. This is missing in forecasting.
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One of the areas where this would be observable are Kaggle-Competitions and EU Nowcasting Competitions.

In such winner-takes-most prize competitions there is a strong incentive to give the best estimate. However, you need to also win. There is an additional incentive to make your forecast stand out, increasing the probability of winning at the cost of making a worse estimate.

See for a great start to this topic:
Witkowski, Jens, et al. “Incentive-compatible forecasting competitions.” Management Science 69.3 (2023): 1354-1374.
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This may be dealt with outside of the forecasting literature in some different context.
How to do it: Gather (resolved) fixed event forecasts that are more than a couple of years out. Check whether predictions are unbiased. Then check how existing bias can be explained and to what degree that bias is likely to come from time preferences. I am attempting this soon.
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This is perhaps already well researched. See e.g.:
King, Owen C., and Mayli Mertens. “Self-fulfilling Prophecy in Practical and Automated Prediction.” Ethical Theory and Moral Practice (2023): 1-26.

However, given that I am not aware of any impact that this has had on real-world decision-making, results may be either unconvincing or poorly communicated. Additional research could be helpful.
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This also works the other way around. Reading the Great Gatsby, one can clearly see some aspects of life that were very different back in the 1920s. I think that economics plays a fundamental role in explaining a lot of variation.
Major social changes in the last 100 years would have been: 1) Democratisation 2) Environmentalism 3) A focus on individual health and well-being 4) increased womens rights + much more. What lies in store in the next 100 years? Have such predictions been made in the past?
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Crowds of experts can forecast whether studies replicate and what likely outcomes are:

DellaVigna, Stefano, Devin Pope, and Eva Vivalt. “Predict science to improve science.” Science 366.6464 (2019): 428-429

This allows us to interpret the estimates provided by studies and counter publication bias.

More importantly, this has wide-ranging consequences for science and policy. It suggests that there are (better) ways to combine expert knowledge on the effects of policy interventions. It also implies that the philosophically delicate topic of causal inference is possible with pure judgment. I do not see any of those implications being explored to a proper extent. I am currently working on this, so reach out to me if this sounds interesting!
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We should clearly use our data on COVID-19 to brace ourselves for the next pandemic. Research should aim to create tools that make it available to nowcast cases at the beginning of a pandemic, when tests are expensive and uncertainty is high. For example, asking about social circles could be an effective method to do this:
Galesic, Mirta, et al. “Human social sensing is an untapped resource for computational social science.” Nature 595.7866 (2021): 214-222.
How do judgmental forecasts and models compare? Do models for COVID-19 work for other pandemics in history too? Should we expect nowcasting ability to carry over to novel pandemics at all?
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A wonderful example of something like this is Robin Hansons Age of Em. The book is simply an exploration of a future in which brain scans and brain emulations are available. Hanson uses standard economic theory as well as physics and sociology to paint a detailed picture of such a future. Astonishingly, by simply applying standard methods Hanson arrives at a relatively concrete and largely convincing scenario that is fundamentally different from the world in 2024 in ways that are not obvious.

Hanson, R. (2016). The age of Em: Work, love, and life when robots rule the Earth. Oxford University Press.
I would love to see the same thing for the scenarios outlined.
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Different fields have fundamentally different ways of thinking about energy forecasts. Natural scientists often tend to focus on the physical and technological limits whereas social scientists usually tend to start with demand for energy. Many long-term forecasts are simple extrapolations of current trends. By gathering forecasts and taking an interdisciplinary perspective new insights and uncertainties could emerge.

See:
Weisz, Paul B. “Basic choices and constraints on long-term energy supplies.” PHYSICS TODAY. 57.7 (2004): 47-52.
Höök, Mikael, et al. “Global coal production outlooks based on a logistic model.” Fuel 89.11 (2010): 3546-3558.
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The Paris climate agreement is not the first and likely not the last. It is unusually unspecific for a climate agreement and is considered low in mechanisms that incentivize lower emissions.

Overall, the effectiveness of the Paris climate agreement seems to be understudied:

Raiser, K., Kornek, U., Flachsland, C., & Lamb, W. F. (2020). Is the Paris Agreement effective? A systematic map of the evidence. Environmental Research Letters, 15(8), 083006.

Furthermore, it would be interesting to understand how and why the Kyoto and Paris agreements differ from the theoretical optimum. How can future agreements be practically improved given the theoretical considerations and emerging evidence?

A great book for this:

Barrett, Scott. Environment and statecraft: The strategy of environmental treaty-making. OUP Oxford, 2003.
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This is an area of current research. That means that additional research can strongly shape future research. Many question need to be discussed on a very fundamental level.

What is the ability of central banks to mitigate climate change? Banks such as the ECB have climate change programmes. Can they be analyzed for their effectiveness?

Is there a moral imperative for central banks to engage in mitigating climate change beyond their (usually) core goal of administering money and overall price levels?

How does climate change influence financial risk? Which long-term relation do central banks assume?
An influential article seems to be:

Dafermos, Yannis, Maria Nikolaidi, and Giorgos Galanis. “Climate change, financial stability and monetary policy.” Ecological Economics 152 (2018): 219-234.

Attacking the problem would first involve understanding how central banks understand and frame the problem. How should central banks frame the problem?

Thiemann, M., Büttner, T., & Kessler, O. (2023). Beyond market neutrality? Central banks and the problem of climate change. Finance and Society, 9(1), 14-34.
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Whats interesting is how the availability of geoengineering will change climate decisions in the future. I find that this line of research is underexplored. We need to accurately model incentives of future decision-makers to make predictions regarding climate change and the (non)-use of geoengineering.

Feel free to contact me regarding this line of research.

See for starters: WAGNER, Gernot. Geoengineering: the gamble. John Wiley & Sons, 2021.
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Clearly, pandemic responses and preventive measures have the basic problem that the nation enforcing them bears all the cost, but others profit. Thus, there is a incentive to free-ride on others lockdowns. Collectively, this should reduce the pandemic responses far below the optimal level. Maybe, International Agreements can address this. Unfortunately, I could not find a good source that seems to cover this.

Studying the collaborations on combating COVID-19 would be interesting. How have countries responded to the incentives and other nations responses? Was free-riding observable?

Developed nations coordinate their fiscal policy in the G20. Given the distant similarity of the problem, could a similar venue and agreements be used to coordinate pandemic responses?
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This overlaps with the section on Futures. I would recommend a similarly straightforward methodology.

See for one example:

Scharre, Paul. Army of none: Autonomous weapons and the future of war. WW Norton & Company, 2018.
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The following paper is a good start. It is a review that emphasizes the importance of research in that area and outlines which additional research can be helpful.

Chadefaux, T. (2017). Conflict forecasting and its limits. Data Science, 1(1-2), 7-17

Simply gathering conflict-related predictions and comparing them would be the next step. Given the Middle-eastern and Ukraine-Russian conflicts we probably have a lot of fresh data that needs analysis.
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The main problem with international agreements is that there is no third party that can punish, reward or otherwise enforce compliance. Therefore, international agreements need to be self-enforcing, i.e. better for all sides involved at all times.
However, we may be able to improve upon this by hard-coding payments, e.g. via a blockchain. If a country violates an agreement, an automatic payment (punishment) could be triggered. The main limitation here clearly is that we still need a third party to decide whether a violation of a contract has obviously occured. However, there is currently no lack of trusted third parties. We could crowdsource that decision to a sufficiently large number of citizens or international courts.
Nelaturu, Keerthi, et al. “On public crowdsource-based mechanisms for a decentralized blockchain oracle.” IEEE Transactions on Engineering Management 67.4 (2020): 1444-1458.
Goel, Naman, et al. “Infochain: A decentralized, trustless and transparent oracle on blockchain.” arXiv preprint arXiv:1908.10258 (2019).
Reinsberg, B. (2021). Fully-automated liberalism? Blockchain technology and international cooperation in an anarchic world. International Theory, 13(2), 287-313.

If this would work, this would greatly increase the possible sets of agreements, thus furthering peace and cooperation.

I am currently investigating main limitations as well as potential applications of this idea.
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In this paper:

Cowen, Tyler, and Ben Southwood. “Is the rate of scientific progress slowing down?.” (2019).
the authors discuss some tentative reasons to believe that ‘progress’ (which may be a broader concept than economic growth encompassing multiple per capita variables) might be slowing down in developed countries. To which extent is this a robust assessment? What could be causes? What could be the consequences?

The german economic advisory panel also predicts several decades of low growth for Germany, speculating on demographic change (overaging) as a primary driver.

The authors discuss the importance of this assessment for philanthropy briefly: Should there be a focus on boosting progress in developed nations or a focus on boosting overall progress—which would focus on developing nations? Whilst progress in developing nations is much easier to come by, boosting progress in developed nations might be instrumentally valuable as these are the nations that hold most of the power on earth.
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1. Many “technologists” repeatedly tout that technological progress is highly non-linear, thus we must expect rapid (even exponential) technological progress in the future.
2. According to standard models of economic growth (and the understanding that they embed), technological progress is the main long-term driver of economic growth in developed countries.
3. Economic growth in developed countries has been constant and low over the last decades. Current long-term projections assume that economic growth will not accelerate or even decelerate.

These beliefs are incompatible. Either technological progress is not accelerating as quickly OR this is not linked to economic growth in the way currently assumed OR long-term projections are erroneous.

My personal conjecture is that technological progress is often exponential when a technology is new. We went from the first heavier-than-air flight in 1903 to jet-powered airliners in the 1950s and the first human in orbit in 1961. However, civil aircraft designs have hardly changed since then, mostly just adapting to higher costs of fuel and labor.
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This is not my field of expertise, but I would have started reading here:

Helleiner, Eric. “Understanding the 2007–2008 global financial crisis: Lessons for scholars of international political economy.” Annual review of political science 14 (2011): 67-87.
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This overlaps with the section on Futures. I would recommend a similarly straightforward methodology.

Developed countries are projected to experience lower growth per capita and even negative growth total because an unusually large share of inhabitants will be retiring in the next decades.

What are the implications of low economic growth for our mid-term future?

This question could be studied statistically, using extrapolation to rearrange power rankings among countries if developed countries do not grow.
Culturally, what happened to Japan as it had no growth for a decade straight?
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The paper:
Trammell, Philip, and Anton Korinek. “Economic growth under transformative AI.” Global Priorities Institute. https://globalprioritiesinstitute.org/philip-trammell-and-anton-korinek-economic-growth-under-transformative-ai (2020).
suggests that we know very little about economic growth under transformative AI. Both explorative and review work is necessary. The paper conveys many angles of attack.
I do not recommend to look at labor market situations, as this has been the primary focus of economists and very much research already exists.
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This question was inspired by this model of takeoff-speeds. There is a lot of uncertainty in the model, and I think it is worth exploring economic growth and AI more in-depth (see previous question). However, I also would like to see a scenario analysis applying standard economics, as in Hanson (2016), not because the particular scenario is likely to happen, but because it may unveil interesting repercussions and considerations. What would happen if 20% of all jobs were automated relatively quickly? How would governments respond (democratic/autocratic)? How would investors buy additional computational power and from whom? How quickly can additional computational power be installed? What would the energy demand be? Which resources would be in high demand? How would it affect the international balance of power? It could be that some of these questions are already well answered somewhere. However, I think that most of the work in economics focuses on labor market models, missing many crucial points.

Hanson, R. (2016). The age of Em: Work, love, and life when robots rule the Earth. Oxford University Press.
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The role of central banks is still much discussed among economists and additional research may help shape central bank policy. See the footnote on green central banking in the climate change section.

Since central banks are interpreting climate change as a threat to economic (and thus price) stability, they are starting to change their policies accordingly. This opens up the possibility that other problems, such as e.g. pandemic preparedness may get a similar treatment. In fact, most pressing problems lead to economic crisis and could thus be understood as a problem that central banks could face. It is far from certain whether this is a good idea. This is itself a very interesting research question. See:

Thiemann, M., Büttner, T., & Kessler, O. (2023). Beyond market neutrality? Central banks and the problem of climate change. Finance and Society, 9(1), 14-34.
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Lührmann, Anna, and Staffan I. Lindberg. “A third wave of autocratization is here: what is new about it?.” Democratization26.7 (2019): 1095-1113.

Well, that sucks! Understanding the current autocratization is not easy. Many tout the importance of social media and how it affects disinformation, but this seems speculative. One important question is whether there is a common reason for autocratization at all.

This question could be attacked with data analysis: Statistically speaking, is the current autocratization significant? Does the data in across countries support the hypothesis that autocratization is driven by a common cause?

How about the first two waves of autocratization? How were they different? How were they similar?

What could be root causes of autocratization on a larger level?
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What do purely predictive takes on autocratization/liberalization predict for our future? I would probably first look at the literature and which models have been used to forecast autocracy. Which predictive models are best? Then I would play around with many others to try to come up with better ones. We now have better regression techniques, such as deep learning aided symbolic regression to attack these problems than a couple of years ago.
Fogel, Robert W. “Capitalism and democracy in 2040: forecasts and speculations.” (2007).
Goldstone, Jack A., et al. “A global model for forecasting political instability.” American journal of political science 54.1 (2010): 190-208.
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Here, it would be best to study history. How have voting methods been (unsuccessfully) introduced in the past? When? By whom and why? How frequently are they changed? How much do changes reflect understanding of the economics of voting methods?
See:
Barbaro, Salvatore. A social-choice perspective on authoritarianism and political polarization. No. 2108. 2021.
See also: https://electionscience.org/learn/
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An interesting start is the methodology of the paper below:
https://forum.effectivealtruism.org/posts/jCwuozHHjeoLPLemB/how-long-do-policy-changes-matter-new-paper
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If autocrats could live forever, this would reduce the probability of switching to a more democratic regime in the future. It would be highly interesting to:
1) Imagine a future in which autocratic regimes do not die of natural causes
2) Explore what the effect of additional length of life is on autocratic stability. Given that longevity has been increasing steadily over the past century, how much of the contemporary autocracy can be explained by increases in longevity?
I have not seen any thorough analysis of this kind, although there is of course some literature investigating the issue. An interesting paper seems to be:

Tanaka, S. (2018). Aging gracefully? Why old autocrats hold competitive elections. Asian Journal of Comparative Politics, 3(1), 81-102.
There are at least two angles-of-attack here:
1 - Theoretical modeling: incorporate longevity into a model where regime changes occur randomly as a function of age/health/death of the autocrat. If this model explains a lot of variance in historical measures of autocracy then there might be something to it.
2 - Empirical analysis: Study (dead) autocrats. Analyze the effect of a leaders death on the following liberalization of a nation using a regression-discontinuity-design. What is the implication of effect sizes for a world with increasing longevity?
For that matter: Are the current measures of autocratization/liberalization good indices? Could their composition confound empirical results?
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A study that strikes me as wonderfully simple, yet effective:
Grodeck, Ben, and Philipp Schoenegger. “Demanding the morally demanding: Experimental evidence on the effects of moral arguments and moral demandingness on charitable giving.” Journal of Behavioral and Experimental Economics 103 (2023): 101988.

We need more of these studies. Which other factors might be at play? (see also the next footnote) Follow-on studies could experiment with actual larger donations to effective charities outside of the lab.
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This question could be resolved by looking at what makes altruists, and what makes them (in)effective.

Jaeger, B., & van Vugt, M. (2022). Psychological barriers to effective altruism: An evolutionary perspective. Current Opinion in Psychology, 44, 130-134.

A great psychology study would take on the loose ends existing in the literature and empirically test them. Furthermore, the research cited above makes some interesting claims as to the causes of ineffective altruism. What does this imply for the future of effective altruism? Does this explain altruistic spending in the past? How credible are the arguments?
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There is a consensus that questionable research practices are highly prevalent. This is bad, as it dilutes the reliability of scientific works. Economic theory readily predicts such behavior. So it should actually come as a surprise how much of science is still powered by truth-seeking. Economic theory also predicts what can be done to align academic incentives with scientific truth-seeking. Which actions can be undertaken that steer academia towards better incentives? Related Literature:

Maxwell, S. E., Lau, M. Y., & Howard, G. S. (2015). Is psychology suffering from a replication crisis? What does “failure to replicate” really mean?. American Psychologist, 70(6), 487.

John, Leslie K., George Loewenstein, and Drazen Prelec. “Measuring the prevalence of questionable research practices with incentives for truth telling.” Psychological science 23.5 (2012): 524-532.
You may also be interested in the Unjournal, which I understand to be another attempt to improve the quality of evaluation of scientific work.

It is very important to work closely with very senior personnel to tackle such a question. Seasoned professors best understand the system, and how to change it.
The difficult part here is not the “how” academia could be better. This is obvious to most people. The important part is to get people to change it. This has happened in the past. Academia has changed. Why? Why are registered reports a thing now, but other attempts to improve e.g. peer-review have failed?

Chambers, C. D., & Tzavella, L. (2022). The past, present and future of registered reports. Nature human behaviour, 6(1), 29-42.
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Given that a philantropic actor should expect to be able to transfer resources across time at market interest rates, it is non-obvious which spending strategy makes sense. This is a core question for altruists and one that has recently received some research. Nonetheless, answers are not yet satisfying.
MacAskill, W. (2019). When Should an Effective Altruist Donate?’. Manuscript in preparation. https://globalprioritiesinstitute.org/wp-content/uploads/William_MacAskill_when-should-an-effective-altruist-donate.pdf
Trammel (2021) https://globalprioritiesinstitute.org/wp-content/uploads/Trammell-Dynamic-Public-Good-Provision-under-Time-Preference-Heterogeneity.pdf

I think that there is a case for much more basic research here, as outlined by the existing research. What is the core problem here? Which problems do existing and related works tackle? How does existential risk play into this?
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There is a lot of literature on this point, but no summary nor review of this. Thus, it would be very valuable if someone could synthesize existing knowledge on this key point.
Start e.g. with:
Cowen, T. (2007). Caring about the distant future: why it matters and what it means. U. Chi. L. Rev., 74, 5.
Gollier, C. (2002). Discounting an uncertain future. Journal of public economics, 85(2), 149-166.
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This could involve, e.g. excessive credit-taking or a large drop in fertility or education, but to answer the question a much more thorough analysis would have to be undertaken.
Financial market interest rates are usually controlled by central banks. Would this still be the case if large shares of the population were discounting the future heavily?
How would (central) banks react to that?
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Germany is currently investigating whether to tax factory farming so as to incentivize better treatment of animals. Whilst there is some research on this (Google Scholar “factory farming tax”), additional top-notch research may be influential in such decisions. Whilst the existing research is focused on ethics, policy-makers are unlikely to be swayed by that. Rather, I believe a standard economic analysis on a textbook-level that explores consequences of such a tax in detail would be valuable. The most interesting point to policy-makers is likely to be how factory farmers will be affected. How much damage will their businesses incur? Which regions will be most affected by this? Making forecasts here would be useful. Is this unprecedented? Has something like this happened in the past/to a different agricultural product? What is the global effect on animal welfare? Is cruel factory farming crowded out to other nations as a result?
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Naveh-Kedem, Yael, and Noga Sverdlik. “Changing prosocial values following an existential threat as a function of political orientation: Understanding the effects of armed conflicts from a terror management perspective.” Personality and Individual Differences 150 (2019): 109494.
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Large Language Models could be fine-tuned to act as if they are human. Whilst this clearly can not replace a lab experiment with actual humans, it may make for an interesting testbed for new lab experiments before they are tried on humans. An implicit example would be:

Schoenegger, P., & Park, P. S. (2023). Large language model prediction capabilities: Evidence from a real-world forecasting tournament. arXiv preprint arXiv:2310.13014.
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I have not looked into this much. A point to start would be:

Demszky, D., Yang, D., Yeager, D. S., Bryan, C. J., Clapper, M., Chandhok, S., … & Pennebaker, J. W. (2023). Using large language models in psychology. Nature Reviews Psychology, 1-14.
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There are different theories of causation. Most economists use the “potential outcomes” framework which does not allow analyses based on assumptions such as the theory of causation by Pearl, “Structural Causal Models”. Pearls model has the major downside that it does not consider effects to be time-dependent, which prohibits many types of analyses. See also the next footnote. However, I will hope that the two have a common nature and are not mere whims of human thought. Thus, the strength of both approaches may be joined.

See:

Pearl, Judea, Madelyn Glymour, and Nicholas P. Jewell. Causal inference in statistics: A primer. John Wiley & Sons, 2016.
Imbens, Guido W. “Potential outcome and directed acyclic graph approaches to causality: Relevance for empirical practice in economics.” Journal of Economic Literature 58.4 (2020): 1129-1179.
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Pearls theory of causality as described in his book “Causality” and the textbook “Causal inference in statistics: A primer”, is a complete theory for determining causality using both plausible assumptions (such as temporal precedence) and experimental evidence (such randomization). However, the theory is void of dynamics, i.e. time-dependence. Thereby, no causal effects that are part of a cyclical system in which a variable affects its future self can be even described, much less estimated. Given that dynamic systems are a standardly modelled in physics (using differential equations) and adjacent areas, is it possible to enhance Pearls theory of causation by adding time-dependence? This would involve making reasonable assumptions about the “response” of variables to one another. But this seems okay: Inflation expectations do not change much from one day to the next, but they will change over a course of 10 years, given a change in inflation.

There seem to have been a lot of attempts to do this, but none of them has made it to textbook level yet. See e.g.:
Bongers, S., Peters, J., Schölkopf, B., & Mooij, J. M. (2016). Theoretical aspects of cyclic structural causal models. arXiv preprint arXiv:1611.06221
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This would likely involve only standard microeconomics. What are the incentives for each of the members at the respective levels?

Whilst there is of course more to being a catholic than simply money and social incentives, economic analysis might explain the decisions made at each level well. Sports players and academic researchers also have more complex interaction that are not solely focused on money and social incentives, but standard economic analysis goes a long way to describe the shortcomings of academia and the behavior of professional sports players.

What motives (hidden or not) explain behavior? How has the church responded to potential reductions in income? Which measures does the church (hidden or not) take to generate income?

Much of the analysis (such as e.g. rent-seeking) that is done for public instituitions could be applicable here.

To my surprise, I have not been able to find any literature in that direction!