In this series on the content of my recent paper on the arXiv (and accepted to Acta Astronautica) I’ve mostly just described ways to do SETI.  I conclude with some highly subjective advice on SETI for those jumping into the field.

1. Read the literature

There are a lot of SETI papers, and very few of them have ever been cited. Going through it as we have for the SETI bibliography, it’s striking how many times the same ideas get discussed and debated without referencing or building on prior work on the topic.

This is partly because the field is scattered across journals and disciplines, and because there’s no curriculum (yet!). The result is a lot of wasted effort.

Fortunately, you can now keep up with the field at seti.news and search the literature at ADS using the bibgroup:SETI search term.

2. Choose theory projects carefully

I was taught by my adviser (who got it from his adviser, George Herbig) to “stay close to the data”. I took this to mean both to always make sure I understood the data and didn’t go chasing data reduction artifacts (I like to try to see strong signals myself, by eye, in the raw data when I can to confirm it’s real), but also to in theory projects really think hard about what the data say, and how it might mislead.

The most useful theory projects are the ones that help searches. A paper that calculates the observability of a particular technosignature using parameters that let observers translate their upper limits into constraints on technologies is staying close to the data.  One speculating on the far future fate of aliens at the edge of the universe—well, it may be very interesting, but it’s not close to the data.

Two topics that I think are probably overrepresented in the literature are the Fermi Paradox and the Drake Equation. Now, I’m very proud of the papers I’m on about the Fermi Paradox, so I won’t say to avoid the topic, but ultimately the Fermi Paradox is not actually a problem that I think demands a solution. Such work also works best when it leads to observational predictions, and so informs searches and the interpretation of data.

But continuing to argue about it after so much ink has been spilled about it, and in a situation where we have so little data to go on, creates diminishing returns. Kathryn Denning describes the “now-elaborate and extensive discourse concerning the Fermi Paradox” as being “quite literally, a substantial body of analysis about nothing, which is now evolving into metaanalysis of nothing.” continuing, “I would not suggest that these intellectual projects are without value, but one can legitimately ask what exactly that value is, and what the discussion is now really about. And, refering to early work on the problem:

Thinking about that future [of contact with ETI] was itself an act of hope. Perhaps it still is. But I want to suggest something else here: that the best way to take that legacy forward is not to keep asking the same questions and elaborating on answers, the contours of which have long been established, and the details of which cannot be filled in until and unless a detection is confirmed. Perhaps this work is nearly done.

I think she’s right, and this goes for work on the “Great Filter” and “Hard Steps” models in SETI, too.

The Drake Equation, similarly, occupies a big chunk of the theory literature. The equation is very useful and in a way sort of defines the field of SETI, but ultimately it’s a heuristic and its purpose is to help us think about our odds of success. But even Frank will tell you that while it’s useful to plug in numbers to get a sense of whether SETI is worthwhile (it is!), it’s not meant to be solved or made exact. It’s not a foundational equation like the Schrodinger equation from which one derives results, it’s more like a schematic map of the landscape to help orient yourself.

So while there’s no problem with using the Drake Equation to illustrate a point or frame a discussion, I think working to refine and make it better is to misunderstand its role in the field.

3. Think about the nine axes of merit

Sofia Sheikh has a very nice paper describing how to qualitatively describe the merit behind a particular technosignature.  When proposing a new technosignature, I recommend thinking about them all, but a one in particular: “ancillary benefits,”. This gets to Dyson’s First Law of SETI Investigations: “Every search for alien civilizations should be planned to give interesting results even when no aliens are discovered.”

There are three reasons for this. The first is the funding paradox that null detections must be used to justify yet more effort. If there are ancillary benefits, then this is easier. The second is that doing other work with the data or instruments you use means you stay connected to the rest of astronomy (this also helps junior researchers get jobs and stay employed). The third is that it’s easy to get discouraged after years of null results. Having something to work on in the meantime helps keep one going.

This point should not be taken too strongly however. Radio data of nearby stars might really have no practical application beyond a null detection, and that’s OK. Those null detections are still good science! Also, the skills one uses to do that search, and the equipment built to do it, are all transferable to interesting astronomy problems.

4. 4. Engage experts

Lots of SETI papers written by physicists (and others) go way outside the authors’ training. There’s a particular tendency among physicists (and others) to feel like since we’re good at physics and physics is hard and everything is fundamentally physics, that we can just jump into a field we know little about and contribute.

Engaging experts in those fields will both help us not make mistakes and broaden the field by bringing them into it so they can see how they can contribute. It’s win win! And we should do it more.

5. Plan for success when designing a search

One should think hard about upper limits and what result one will have when one is done searching before one starts the search. This is easier said than done, but really helps sharpen one’s work, and ensures that a useful result will come out at the end.

It also helps draw in experts! A SETI skeptic might not want to help you, say, look for structures on Mars lest they be drawn into another Face on Mars fiasco, but if they see that they’re contributing to an upper limit (that confirms their priors!) on such faces, they will be more likely to really help.

6. Stay broad minded

We all come to the problem of SETI with very different priors for how SETI can succeed, and so will invariably encounter practitioners pursing what we feel are very unlikely or misguided paths to success. It helps to remember that the feeling may be mutual

In particular, we can acknowledge the value in the exercise of, say, considering ‘Oumuamua as an alien spacecraft without falling into the “aliens of the gaps” trap. That is we should distinguish between claims that

1. Our prior on a particular technosignature is too small, using a particular case study as an example, and
2. A particular case study is likely to be a technosignature

The first is entirely appropriate. Before ‘Oumuamua, I did not think much about the possibility of alien spacecraft in the solar system. Now, I think I have a much better informed prior on the likelihood and form of such a thing.

The second requires extraordinary evidence because our prior on such a thing is (presumably) quite small.

7. Stay skeptical, but not cynical

I’ll close by just quoting the end of my paper:

Not all SETI researchers believe they will have a good chance of success in their lifetimes, but such a belief surely animates much of the field. It can therefore be challenging to maintain a scientist’s proper, healthy skepticism about one’s own work, especially when coming across a particularly intriguing signal.

I suspect everyone who engages in the practice long enough will come across what looks to be a Wow! Signal and, at least briefly, dream of the success that will follow. The proper response to such a discovery is a stance of extreme skepticism: if one is not one’s own harshest critic, one may end up embarrassing oneself, and losing credibility for the field. It is at these moments that Sagan’s maxim should have its strongest force.But one should also not let the product of such false alarms be a cynicism that leads one to focus entirely on upper limits and dismiss all candidate signals before they are thoroughly examined as just so much noise. There is a wonder that brought many of us into the field that must be nurtured and protected against the discouragement of years or decades of null results that Drake warned about. One should cherish each false alarm and “Huh? signal” as an opportunity for hope and curiosity to flourish, “till human voices wake us, and we drown.”

 

You can find the paper here.