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I had a discussion with my advisor about what am I interested as my future research direction and I said it is special functions and q-series. He laughed and said that the topic is essentially dead and the people who study it are dinosaurs. I'm really confused by this statement and don't know what to think. Is this area really dead and not worth pursuing a research in it?

I cannot answer the question of whether the field of $q$-series is dead. I would make this a comment, but I lack sufficient reputation.

I am a Banach space theorist, and Banach space theory is not fully dead. However, it is sufficiently unfashionable as to make it terribly difficult for me to find a job (even with a very strong research record). In fact, I have been completely unable to find employment, and I am now forced to leave academia because of it. Granted, geographical factors, personal connections, and luck may all be different for you. However, I made the mistake of choosing my research area only because of its intellectual interest to me, without any practical consideration of the job market, and I would caution you against doing the same. If your advisor says the area is dead, I would listen.

I would also say that, if you like that area, you can study it as much as you want after you find a permanent position.

Jehanne Dousse has recently obtained a sought-after CNRS position. From what I remember seeing, she was inundated with job interviews. This should disprove the death of q-series, at least as far as partition-like series are concerned. Certain subfields may be worse off.

If you want to discreetly ask specific people inside the field whether the field is alive enough to support a career, a good approach seems to me to state the question positively: Ask what the most interesting currently existing questions are, what the most exciting recent work is about, etc. With some luck you may get a good research project in return :)

The opinions that certain areas of mathematics are dead are frequently stated but in many cases incorrect. Some areas experience declines in activity and then revivals. Many examples can be given.

On the other hand, my recommendation to a PhD student would be: do what your adviser says. When you obtain a permanent position you will be free to pursue whatever topic you yourself find interesting. Until that time you have to take into account various things other than intrinsic interest of the topic.

Example. In the early 1980th my friend, then a graduate student, discussed with his adviser possible directions of research. The adviser himself contributed to classical complex functions theory and to holomorphic dynamics. He said that holomorphic dynamics is dead, and recommended to
work in classical function theory (the area which was not the most popular at that time either). It is almost exactly at that time (1982) when the revolution in holomorphic dynamics happened, suddenly this become one of the most fashionable area in whole mathematics, and it preserves this status to this day. But in 1960-80 the adviser was almost alone, working in holomorphic dynamics.

The reports of the death of the field of $q$-series and special functions are greatly exaggerated. George Andrews wrote a book Q-Series on the subject published in 1986. He and Bruce Berndt last year completed the publication of a five volume edition about the results in Ramanujan's Lost Notebook. An important subject for Ramanujan was $q$-series and special functions. George Andrews is a former President of the AMS with many awards.

Ken Ono, the Vice President of the AMS, has done research on Rogers-Ramanujan identities, Mock theta functions, and recently he and his coworkers have proved the Umbral Moonshine Conjecture. In joint work with Jan Bruinier, he discovered a finite algebraic formula for computing partition numbers. The partition numbers are the coefficients of the reciprocal of the fundamental $q$-series $(q;q)_infty$. There are many other examples that I could cite, but this should be enough.

I think that (properly understood) theory of $q-$series is one of the most fashionable areas of mathematics right now. One reason is the appearance of $q-$series in topology. Namely, Turaev-Viro TQFT associates to each $3-$manifold with boundary a $q-$special function, defined for $q$ being a root of unity. These functions are expected to be $q-$holonomic, so should satisfy interesting difference equations. The building block for these invariants is so-called quantum $6j-$symbol, which coincides with $_4F_3-$ basic hypergeometric series with general parameters at $z=1$.