Do computer scientists care about the complexity of specific games still?

(Expanding my comment.)

I think your assessment is correct -- it's much harder to publish results of the form "game X is NP-hard" today than it was last century -- although it is not something I've looked into.

I think the reason for this is the following.

The first few examples of NP-hard games are interesting. It means we can say "many games turn out to be NP-hard". That helps motivate research on NP-hardness and helps scientific communication with the general public.

However, once, say, half a dozen examples have been established, what is the value of adding more examples? Of course, there is value in having more examples, but it becomes more marginal. Each successive example is less surprising and doesn't really change the above statement.

Moreover, many of these proofs are quite messy -- not the sort of thing a reviewer is keen to work through.

Note that this phenomenon is not exclusive to results about games. I think there are many papers that struggle to get published today even though they'd sail in 30 years ago. For example, Karp's 21 NP-complete problems is a celebrated paper, but a similar list of NP-complete problems would struggle to get published today. The reason is simply that those 21 examples were surprising then, but are not today.

An important side note: In essentially all examples, the original game is not NP-hard because it has a finite, albeit extremely large, state space. Thus the NP-hardness is proved about some generalization of the game. Such as Chess on n-by-n boards with slightly modified rules.

I'm going to say that your assessment isn't correct (point 1). I'd also suggest that the Mathematics site here might be an even better venue for a question such as this. Here is why.

It isn't so much that game theory (complexity, solvability, completeness, ...) isn't interesting any more, but that it is the techniques applied to any given game can be new or old. The same is true of Mathematics in general. If I prove a new and wonderful theorem of any sort in math or cs, using "well-worn" techniques, it won't be interesting to very many people. You can make a lot of cookies with a a good cookie cutter. However, if I prove something with a novel and previously unknown attack, people will go wild. Well, those deep in the particular weeds of that field anyway. Whoa, a bitcoin powered AI cookie cutter. (Sorry.)

My own work from long ago is an example (Math Analysis). At the time I wrote it there were only about five people in the world who could read and analyze it comfortably, including myself and my advisor. I say that just to indicate how obscure a sub-topic it was, not to suggest anything about my ability. The main result was "very nice and a bit more than most dissertations offered", so said another professor who tried to grasp it (a committee member). So far, no big deal. However, the main result used a completely new methodology and a seemingly orthogonal attack on the problem. That is what made it interesting enough to be published in Trans. AMS. It just wasn't the sort of thing that would occur as a matter of course to others, even weed-dwellers.

On the other hand, it was getting extremely difficult to prove much of anything in that small area then as the ground had been so well trodden. The study of Analysis moved on to other areas in which less was known and more could be learned. Suddenly there were lots of papers in the new direction and few in my chosen somewhat weedy field.

But a paper now, to be published in Classical Real Analysis, has to be quite interesting in its techniques, not just its results, unless, of course, it concerns a classic unsolved problem.

So, I think the issue isn't whether games are interesting or not. It is what is new that you can show about how to attack an interesting game. And the problem gets harder and harder as the field gets more and more "trodden."

But that, I think, is true of any mathematical field, including much of theoretical computer science. Show us a new way to attack problems and we will wake up.